I am overseas the coming week, giving a seminar at Perimeter Institute on Tuesday, a colloq in Toronto on Wednesday, and on Thursday I am scheduled to “make sense of mind-blowing physics” with Natalie Wolchover in New York. The latter event, I am told, has a live webcast starting at 6:30 pm Eastern, so dial in if you fancy seeing my new haircut. (Short again.)
Please be warned that things on this blog will go very slowly while I am away. On this occasion I want to remind you that I have comment moderation turned on. This means comments will not appear until I manually approve them. I usually check the queue at least once per day.
(The above image is the announcement for the New York event. Find the seven layout blunders.)
Sunday, November 12, 2017
Friday, November 10, 2017
Naturalness is dead. Long live naturalness.
But disillusionment followed swiftly when I read the paper.
Gian Francesco Giudice is a theoretical physicist at CERN. He is maybe not the most prominent member of his species, but he has been extremely influential in establishing “naturalness” as a criterion to select worthwhile theories of particle physics. Together with Riccardo Barbieri, Giudice wrote one of the pioneering papers on how to quantify naturalness, thereby significantly contributing to the belief that it is a scientific criterion. To date the paper has been cited more than 1000 times.
Giudice was also the first person I interviewed for my upcoming book about the relevance of arguments from beauty in particle physics. It became clear to me quickly, however, that he does not think naturalness is an argument from beauty. Instead, Giudice, like many in the field, believes the criterion is mathematically well-defined. When I saw his new paper, I hoped he’d come around to see the mistake. But I was overly optimistic.
As Giudice makes pretty clear in the paper, he still thinks that “naturalness is a well-defined concept.” I have previously explained why that is wrong, or rather why, if you make naturalness well-defined, it becomes meaningless. A quick walk through the argument goes as follows.
Naturalness in quantum field theories – ie, theories of the type of the standard model of particle physics – means that a theory at low energies does not sensitively depend on the choice of parameters at high energies. I often hear people say this means that “the high-energy physics decouples.” But note that changing the parameters of a theory is not a physical process. The parameters are whatever they are.
The processes that are physically possible at high energies decouple whenever effective field theories work, pretty much by definition of what it means to have an effective theory. But this is not the decoupling that naturalness relies on. To quantify naturalness you move around between theories in an abstract theory space. This is very similar to moving around in the landscape of the multiverse. Indeed, it is probably not a coincidence that both ideas became popular around the same time, in the mid 1990s.
If you now want to quantify how sensitively a theory at low energy depends on the choice of parameters at high energies, you first have to define the probability for making such choices. This means you need a probability distribution on theory space. Yes, it’s the exact same problem you also have for inflation and in the multiverse.
In most papers on naturalness, however, the probability distribution is left unspecified which implicitly means one chooses a uniform distribution over an interval of about length 1. The typical justification for this is that once you factor out all dimensionful parameters, you should only have numbers of order 1 left. It is with this assumption that naturalness becomes meaningless because you have now simply postulated that numbers of order 1 are better than other numbers.
You wanted to avoid arbitrary choices, but in the end you had to make an arbitrary choice. This turns the whole idea ad absurdum.
That you have to hand-select a probability distribution to make naturalness well-defined used to be well-known. One of the early papers on the topic clearly states
“The “theoretical license” at one’s discretion when making this choice [for the probability distribution] necessarily introduces an element of arbitrariness to the construction.”
Anderson and Castano, Phys. Lett. B 347:300-308 (1995)
Giudice too mentions “statistical comparisons” on theory space, so I am sure he is aware of the need to define the distribution. He also writes, however, that “naturalness is an inescapable consequence of the ingredients generally used to construct effective field theories.” But of course it is not. If it was, why make it an additional requirement?
(At this point usually someone starts quoting the decoupling theorem. In case you are that person let me say that a) no one has used mass-dependent regularization schemes since the 1980s for good reasons, and b) not only is it questionable to assume perturbative renormalizability, we actually know that gravity isn’t perturbatively renormalizable. In other words, it’s an irrelevant objection, so please let me go on.)
In his paper, Giudice further claims that “naturalness has been a good guiding principle” which is a strange thing to say about a principle that has led to merely one successful prediction but at least three failed predictions, more if you count other numerical coincidences that physicists obsess about like the WIMP miracle or gauge coupling unification. The tale of the “good guiding principle” is one of the peculiar myths that gets passed around in communities until everyone believes it.
Having said that, Giudice’s paper also contains some good points. He suggests, for example, that the use of symmetry principles in the foundations of physics might have outlasted its use. Symmetries might just be emergent at low energies. This is a fairly old idea which goes back at least to the 1980s, but it’s still considered outlandish by most particle physicists. (I discuss it in my book, too.)
Giudice furthermore points out that in case your high energy physics mixes with the low energy physics (commonly referred to as “UV/IR mixing”) it’s not clear what naturalness even means. Since this mixing is believed to be a common feature of non-commutative geometries and quite possibly quantum gravity in general, I have picked people’s brains on this for some years. But I only got shoulder shrugs, and I am none the wiser today. Giudice in his paper also doesn’t have much to say about the consequences other than that it is “a big source of confusion,” on which I totally agree.
But the conclusion that Giudice comes to at the end of his paper seems to be the exact opposite of mine.
I believe what is needed for progress in the foundations of physics is more mathematical rigor. Obsessing about ill-defined criteria like naturalness that don’t even make good working hypotheses isn’t helpful. And it would serve particle physicists well to identify their previous mistakes in order to avoid repeating them. I dearly hope they will not just replace one beauty-criterion by another.
Giudice on the other hand thinks that “we need pure unbridled speculation, driven by imagination and vision.” Which sounds great, except that theoretical particle physics has not exactly suffered from a dearth of speculation. Instead, it has suffered from a lack of sound logic.
Be that as it may, I found the paper insightful in many regards. I certainly agree that this is a time of crisis but that this is also an opportunity for change to the better. Giudice’s paper is very timely. It is also merely moderately technical, so I encourage you to give it a read yourself.
Monday, November 06, 2017
How Popper killed Particle Physics
Popper, upside-down. Image: Wikipedia. |
And luckily so, because it was utterly impractical. In practice, scientists can’t falsify theories. That’s because any theory can be amended in hindsight so that it fits new data. Don’t roll your eyes – updating your knowledge in response to new information is scientifically entirely sound procedure.
So, no, you can’t falsify theories. Never could. You could still fit planetary orbits with a quadrillion of epicycles or invent a luminiferous aether which just exactly mimics special relativity. Of course no one in their right mind does that. That’s because repeatedly fixed theories become hideously difficult, not to mention hideous, period. What happens instead of falsification is that scientists transition to simpler explanations.
To be fair, I think Popper in his later years backpedaled from his early theses. But many physicists not only still believe in Popper, they also opportunistically misinterpret the original Popper.
Even in his worst moments Popper never said a theory is scientific just because it’s falsifiable. That’s Popper upside-down and clearly nonsense. Unfortunately, upside-down Popper now drives theory-development, both in cosmology and in high energy physics.
It’s not hard to come up with theories that are falsifiable but not scientific. By scientific I mean the theory has a reasonable chance of accurately describing nature. (Strictly speaking it’s not an either/or criterion until one quantifies “reasonable chance” but it will suffice for the present purpose.)
I may predict for example, that Donald Trump will be shot by an elderly lady before his first term is over. That’s compatible with present knowledge and totally falsifiable. But chances it’s correct are basically zero and that makes it a prophecy, not a scientific theory.
The idea that falsifiability is sufficient to make a theory scientific is an argument I hear frequently from amateur physicists. “But you can test it!” they insist. Then they explain how their theory reworks the quantum or what have you. And post their insights in all-caps on my time-line. Indeed, as I am writing this, a comment comes in: “A good idea need only be testable,” says Uncle Al. Sorry, Uncle, but that’s rubbish.
You’d think that scientists know better. But two years ago I sat in a talk by Professor Lisa Randall who spoke about how dark matter killed the dinosaurs. Srsly. This was when I realized the very same mistake befalls professional particle physicists. Upside-down Popper is a widely-spread malaise.
Randall, you see, has a theory for particle dark matter with some interaction that allows the dark matter to clump within galaxies and form disks similar to normal matter. Our solar system, so the idea, periodically passes through the dark matter disk, which then causes extinction events. Or something like that.
Frankly I can’t recall the details, but they’re not so relevant. I’m just telling you this because someone asked “Why these dark matter particles? Why this interaction?” To which Randall’s answer was (I paraphrase) I don’t know but you can test it.
I don’t mean to pick on her specifically, it just so happens that this talk was the moment I understood what’s wrong with the argument. Falsifiability alone doesn’t make a theory scientific.
If the only argument that speaks for your idea is that it’s compatible with present data and makes a testable prediction, that’s not enough. My idea that Trump will get shot is totally compatible with all we presently know. And it does make a testable prediction. But it will not enter the annals of science, and why is that? Because you can effortlessly produce some million similar prophecies.
In the foundations of physics, compatibility with existing data is a high bar to jump, or so they want you to believe. That’s because if you cook up a new theory you first have to reproduce all achievements of the already established theories. This bar you will not jump unless you actually understand the present theories, which is why it’s safe to ignore the all-caps insights on my timeline.
But you can learn how to jump the bar. Granted, it will take you a decade. But after this you know all the contemporary techniques to mass-produce “theories” that are compatible with the established theories and make eternally amendable predictions for future experiments. In my upcoming book, I refer to these techniques as “the hidden rules of physics.”
These hidden rules tell you how to add particles to the standard model and then make it difficult to measure them, or add fields to general relativity and then explain why we can’t see them, and so on. Once you know how to do that, you’ll jump the bar every time. All you have to do then is twiddle the details so that your predictions are just about to become measureable in the next, say, 5 years. And if the predictions don’t work out, you’ll fiddle again.
And that’s what most theorists and phenomenologists in high energy physics live from today.
There are so many of these made-up theories now that the chances any one of them is correct are basically zero. There are infinitely many “hidden sectors” of particles and fields that you can invent and then couple so lightly that you can’t measure them or make them so heavy that you need a larger collider to produce them. The quality criteria are incredibly low, getting lower by the day. It’s a race to the bottom. And the bottom might be at asymptotically minus infinity.
This overproduction of worthless predictions is the theoreticians’ version of p-value hacking. To get away with it, you just never tell anyone how many models you tried that didn’t work as desired. You fumble things together until everything looks nice and then the community will approve. It’ll get published. You can give talks about it. That’s because you have met the current quality standard. You see this happen both in particle physics and in cosmology and, more recently, also in quantum gravity.
This nonsense has been going on for so long, no one sees anything wrong with it. And note how very similar this is to the dismal situation in psychology and the other life-sciences, where abusing statistics had become so common it was just normal practice. How long will it take for theoretical physicists to admit they have problems too?
Some of you may recall the book of philosopher Richard Dawid who claimed that the absence of alternatives speaks for string theory. This argument is wrong of course. To begin with there are alternatives to string theory, just that Richard conveniently doesn’t discuss them. But what’s more important is that there could be many alternatives that we do not know of. Richard bases his arguments on Bayesian reasoning and in this case the unknown number of unknown alternatives renders his no-alternative argument unusable.
But a variant of this argument illuminates what speaks against, rather than for, a theory. Let me call it the “Too Many Alternatives Argument.”
In this argument you don’t want to show that the probability for one particular theory is large, but that the probability for any particular theory is small. You can do this even though you still don’t know the total number of alternatives because you know there are at least as many alternatives as the ones that were published. This probabilistic estimate will tell you that the more alternatives have been found, the smaller the chances that any one of them is correct.
Really you don’t need Bayesian mysticism to see the logic, but it makes it sound more sciency. The point is that the easier it is to come up with predictions the lower their predictive value.
Duh, you say. I hear you. How come particle physicist think this is good scientific practice? It’s because of upside-down Popper! They make falsifiable predictions – and they believe that’s enough.
Yes, I know. I’m well on the way to make myself the most-hated person in high energy physics. It’s no fun. But look, even psychologists have addressed their problems by introducing better quality criteria. If they can do it, so can we.
At least I hope we can.
Thursday, November 02, 2017
Book Review: Max Tegmark “Our Mathematical Universe”
Our Mathematical Universe: My Quest for the Ultimate Nature of Reality
Knopf (January 2014)
Max Tegmark just published his second book, “Life 3.0.” I gracefully declined reviewing it, seeing that three years weren’t sufficient to finish his first book. But thusly reminded of my shortfall, I made another attempt and finally got to the end. So here’s a late review or, if you haven’t made it through in three years either, a summary.
Tegmark is a cosmologist at MIT and his first book, “Our Mathematical Universe,” is about the idea that the world is not merely described by mathematics, but actually made of mathematics.
I told you ten years ago why this is nonsense and haven’t changed my mind since. It was therefore pretty clear I wouldn’t be fond of Max’s message.
But. Well. People like Max don’t grow on trees. I have much sympathy for his free-range ideas and also, even though I’ve met him several times, I never really figured out what he was tenured for. Probably not the mathematical universe. Once upon a time, I was sure, he must have done actual physics.
Indeed, as the book reveals, Tegmark did CMB analysis before everyone else did it. This solid scientific ground is also where he begins his story: With engaging explanations of contemporary cosmology, the evolution of the universe, general relativity, and all that. He then moves on to inflation, eternal inflation and the multiverse, to quantum mechanics in general and the many worlds interpretation in particular. After this, he comes to the book’s main theme, the mathematical universe hypothesis. At that point we’re at page 250 or so.
Tegmark writes well. He uses helpful analogies and sprinkles some personal anecdotes which makes the topic more digestible. The book also has a lot of figures, about half of which are helpful. I believe I have seen most of them on his slides.
Throughout the book, Tegmark is careful to point out where he leaves behind established science and crosses over into speculation. However, by extrapolating from the biased sample of people-he-spends-time-with, Tegmark seems to have come to believe the multiverse is much more accepted than is the case. Still, it is certainly a topic that is much discussed and worth writing about.
But even though Tegmark’s story flows nicely, I got stuck over and over again. The problem isn’t that the book is badly written. The problem is that, to paraphrase John Mellencamp, the book goes on long after the thrill of reading is gone.
Already in the first parts of the book, Tegmark displays an unfortunate tendency to clutter his arguments with dispensable asides. I got the impression he is so excited about writing that, while at it, he just also has to mention this other thing that he once worked on, and that great idea he had which didn’t work, and why that didn’t work, and how that connects with yet something else. And did I mention that? By the way, let me add this. Which is related to that. And a good friend of mine thinks so. But I don’t think so. And so on.
And then, just when you think the worst is over, Tegmark goes on to tell you what he thinks about alien life and consciousness and asteroid impacts and nuclear war and artificial intelligence.
To me, his writing exhibits a familiar dilemma. If you’ve spent years thinking about a topic, the major challenge isn’t deciding what to tell the reader. It’s deciding what to not tell them. And while some readers may welcome Tegmark’s excursions, I suspect that many of them will have trouble seeing the connections that he, without any doubt, sees so clearly.
As to the content. The major problems with Max’s idea that the universe is made of mathematics rather than merely described by mathematics are:
There. I’ve done it again. I set out with the best intention to say nice things, but all that comes out is “wrong, wrong, wrong.”
To work off my guilt, I’ll now have to buy his new book too. Check back in three years.
Knopf (January 2014)
Max Tegmark just published his second book, “Life 3.0.” I gracefully declined reviewing it, seeing that three years weren’t sufficient to finish his first book. But thusly reminded of my shortfall, I made another attempt and finally got to the end. So here’s a late review or, if you haven’t made it through in three years either, a summary.
Tegmark is a cosmologist at MIT and his first book, “Our Mathematical Universe,” is about the idea that the world is not merely described by mathematics, but actually made of mathematics.
I told you ten years ago why this is nonsense and haven’t changed my mind since. It was therefore pretty clear I wouldn’t be fond of Max’s message.
But. Well. People like Max don’t grow on trees. I have much sympathy for his free-range ideas and also, even though I’ve met him several times, I never really figured out what he was tenured for. Probably not the mathematical universe. Once upon a time, I was sure, he must have done actual physics.
Indeed, as the book reveals, Tegmark did CMB analysis before everyone else did it. This solid scientific ground is also where he begins his story: With engaging explanations of contemporary cosmology, the evolution of the universe, general relativity, and all that. He then moves on to inflation, eternal inflation and the multiverse, to quantum mechanics in general and the many worlds interpretation in particular. After this, he comes to the book’s main theme, the mathematical universe hypothesis. At that point we’re at page 250 or so.
Tegmark writes well. He uses helpful analogies and sprinkles some personal anecdotes which makes the topic more digestible. The book also has a lot of figures, about half of which are helpful. I believe I have seen most of them on his slides.
Throughout the book, Tegmark is careful to point out where he leaves behind established science and crosses over into speculation. However, by extrapolating from the biased sample of people-he-spends-time-with, Tegmark seems to have come to believe the multiverse is much more accepted than is the case. Still, it is certainly a topic that is much discussed and worth writing about.
But even though Tegmark’s story flows nicely, I got stuck over and over again. The problem isn’t that the book is badly written. The problem is that, to paraphrase John Mellencamp, the book goes on long after the thrill of reading is gone.
Already in the first parts of the book, Tegmark displays an unfortunate tendency to clutter his arguments with dispensable asides. I got the impression he is so excited about writing that, while at it, he just also has to mention this other thing that he once worked on, and that great idea he had which didn’t work, and why that didn’t work, and how that connects with yet something else. And did I mention that? By the way, let me add this. Which is related to that. And a good friend of mine thinks so. But I don’t think so. And so on.
And then, just when you think the worst is over, Tegmark goes on to tell you what he thinks about alien life and consciousness and asteroid impacts and nuclear war and artificial intelligence.
To me, his writing exhibits a familiar dilemma. If you’ve spent years thinking about a topic, the major challenge isn’t deciding what to tell the reader. It’s deciding what to not tell them. And while some readers may welcome Tegmark’s excursions, I suspect that many of them will have trouble seeing the connections that he, without any doubt, sees so clearly.
As to the content. The major problems with Max’s idea that the universe is made of mathematics rather than merely described by mathematics are:
- The hypothesis is ill-defined without explaining what “is real” means. I therefore don’t know what’s the point even talking about it.
- Leaving this aside, Max erroneously thinks it’s the simplest explanation for why mathematics is so useful, and hence supported by Ockham’s razor (though he doesn’t explicitly say so).
The argument is that if reality is merely described by mathematics rather than actually made of mathematics, then one needs an additional criterion to define what makes some things real and others not.
But that argument is logically wrong. Saying that the universe is accurately described by mathematics makes no assumption about whether it “really is” mathematics (scare quotes to remind you that that’s ill-defined). It is unnecessary to specify whether the universe is mathematics or is something more, evidenced by scientists never bothering with such a specification. Ockham’s razor thus speaks against the mathematical universe.
- He claims that a theory which is devoid of “human baggage” must be formulated in mathematics. I challenge you to prove this, preferably without using human baggage. If that was too meta: Just because we don’t know anything better than math to describe nature doesn’t mean there is nothing.
- Max also erroneously thinks, or at least claims in the book, that the mathematical universe hypothesis is testable. Because, so he writes, it predicts that we will continue to find mathematical descriptions for natural phenomena.
But of course if there was something for which we do not manage to find a mathematical description, that would never prove the mathematical universe wrong. After all, it might merely mean we were too dumb to figure out the math. Now that I think of it, maybe our failure to quantize gravity falsifies the mathematical universe.
There. I’ve done it again. I set out with the best intention to say nice things, but all that comes out is “wrong, wrong, wrong.”
To work off my guilt, I’ll now have to buy his new book too. Check back in three years.
Saturday, October 28, 2017
No, you still cannot probe quantum gravity with quantum optics
Srsly? |
First things first, why are you still following phys.org?
Second, the paper in question is on the arXiv and is titled “Probing noncommutative theories with quantum optical experiments.” The paper is as wrong as a very similar paper was in 2012.
It is correct that noncommutative geometry plays a role in many approaches to quantum gravity and it’s not an entirely uninteresting idea. However, the variant that the authors want to test in the paper is not of the commonly discussed type. They want the effect to be relevant for the center-of-mass coordinates, so that it scales with the total mass. That assumption has no support from any approach to quantum gravity. It’s made-up. It is also mathematically highly problematic.
Third, I already spelled out in my review several years ago that this is bogus (see section 4.6) and doesn’t follow from anything. Though the academically correct phrase I used there is “should be regarded with caution.”
Fourth, note that the paper appeared on the arxiv two weeks after being accepted for publication. The authors clearly were not keen on any comment by any blogger before they had made it through peer review.
Fifth, let me mention that one of the authors of the paper, Mir Faizal, is not unknown to readers of this blog. We last heard of him when claimed that Loop Quantum Gravity violates the Holographic Principle (it doesn't). Before that, he claimed that the LHC will make contact to parallell universes (it won’t) and that black holes don’t exist (they do).
I rest my case.
And don’t forget to unfollow phys.org.
Wednesday, October 25, 2017
Book Update
As you probably noticed from the uptick in blogposts, I’ve finished writing the book. The publication date is set for June 12, 2018. We have a cover image now:
and we have an Amazon page, where you can preoder my masterwork.
The publishing business continues to surprise me. I have no idea who wrote the text accompanying the Amazon page and, for all I can tell, the first sentence doesn’t even make sense grammatically. Neither, for that matter, did I have anything to do with the cover image. But well, it’s dark, which is fitting enough.
The book is about the role of arguments from beauty, naturalness, and elegance in the foundations of physics, by which I mean high energy physics, cosmology, quantum gravity, and quantum foundations. Or at least that’s what I thought the book would be about. What the book really is about is how to abuse mathematics while pretending to do science.
The structure I chose is somewhat unusual for a popular science book. It’s a series of interviews I conducted, interlaced with explanations of the subject matter, and a broader narrative for context. Among the people I interviewed are Nima Arkani-Hamed, Frank Wilczek, Steven Weinberg, Garrett Lisi, and George Ellis.
You see, I did everything I could to make sure you really, really had to buy the book.
I also interviewed Gian Francesco Giudice, who is maybe not as well-known as the above-named, but who has been a key figure in the naturalness-movement in high-energy physics. Interestingly, he just yesterday posted a paper on the arXiv on what is also a central theme in the book.
To complete the list of interviewees: I also spoke to Michael KrÃ¤mer, a SUSY phenomenologist in Aachen who unwittingly set me off on this whole enterprise, Keith Olive (also a high-energy phenomenologist), Joe Polchinski (a string theorist), Gordon Kane (the only person on the planet able to derive predictions from string theory), Katherine Mack (an astrophysicist), Chad Orzel (he who teaches physics to dogs), Xiao Gang-Wen (a condensed matter physicist with a theory of everything) and Doyne Farmer (a physicist turned economist).
I also interviewed Howard Baer and Gerard 't Hooft, but the two didn’t make the final cut and only appear in a short sentence each. I swear, throwing them out was the hardest part of writing the whole book.
While the book focuses on physics, my aim is much more general. The current situation in the foundations of physics is a vivid example for how science fails to self-correct. The reasons for this failure, as I lay out in the book, are unaddressed social and cognitive biases. But this isn't a problem specific to the foundations of physics. It’s a problem that befalls all disciplines, just that in my area the prevalence of not-so-scientific thinking is particularly obvious due to the lack of data.
This isn’t a nice book and sadly it’s foreseeable most of my colleagues will hate it. By writing it, I waived my hopes of ever getting tenure. This didn’t come easily to me. But I have waited two decades for things to change and they didn’t change and I came to conclude at the very least I can point at the problems I see.
If you care about progress in the foundations of physics, please preorder the book. Also follow me on facebook or twitter for further updates. You don’t have to wait for the book’s content to appear on this blog, it won’t happen.
and we have an Amazon page, where you can preoder my masterwork.
The publishing business continues to surprise me. I have no idea who wrote the text accompanying the Amazon page and, for all I can tell, the first sentence doesn’t even make sense grammatically. Neither, for that matter, did I have anything to do with the cover image. But well, it’s dark, which is fitting enough.
The book is about the role of arguments from beauty, naturalness, and elegance in the foundations of physics, by which I mean high energy physics, cosmology, quantum gravity, and quantum foundations. Or at least that’s what I thought the book would be about. What the book really is about is how to abuse mathematics while pretending to do science.
The structure I chose is somewhat unusual for a popular science book. It’s a series of interviews I conducted, interlaced with explanations of the subject matter, and a broader narrative for context. Among the people I interviewed are Nima Arkani-Hamed, Frank Wilczek, Steven Weinberg, Garrett Lisi, and George Ellis.
You see, I did everything I could to make sure you really, really had to buy the book.
I also interviewed Gian Francesco Giudice, who is maybe not as well-known as the above-named, but who has been a key figure in the naturalness-movement in high-energy physics. Interestingly, he just yesterday posted a paper on the arXiv on what is also a central theme in the book.
To complete the list of interviewees: I also spoke to Michael KrÃ¤mer, a SUSY phenomenologist in Aachen who unwittingly set me off on this whole enterprise, Keith Olive (also a high-energy phenomenologist), Joe Polchinski (a string theorist), Gordon Kane (the only person on the planet able to derive predictions from string theory), Katherine Mack (an astrophysicist), Chad Orzel (he who teaches physics to dogs), Xiao Gang-Wen (a condensed matter physicist with a theory of everything) and Doyne Farmer (a physicist turned economist).
I also interviewed Howard Baer and Gerard 't Hooft, but the two didn’t make the final cut and only appear in a short sentence each. I swear, throwing them out was the hardest part of writing the whole book.
While the book focuses on physics, my aim is much more general. The current situation in the foundations of physics is a vivid example for how science fails to self-correct. The reasons for this failure, as I lay out in the book, are unaddressed social and cognitive biases. But this isn't a problem specific to the foundations of physics. It’s a problem that befalls all disciplines, just that in my area the prevalence of not-so-scientific thinking is particularly obvious due to the lack of data.
This isn’t a nice book and sadly it’s foreseeable most of my colleagues will hate it. By writing it, I waived my hopes of ever getting tenure. This didn’t come easily to me. But I have waited two decades for things to change and they didn’t change and I came to conclude at the very least I can point at the problems I see.
If you care about progress in the foundations of physics, please preorder the book. Also follow me on facebook or twitter for further updates. You don’t have to wait for the book’s content to appear on this blog, it won’t happen.
Sunday, October 22, 2017
New gravitational wave detection with optical counterpart rules out some dark matter alternatives
The recently reported gravitational wave detection, GW170817, was accompanied by electromagnetic radiation. Both signals arrived on Earth almost simultaneously, within a time-window of a few seconds. This is a big problem for some alternatives to dark matter as this new paper lays out:
The observation is difficult to explain with some variants of modified gravity because in these models electromagnetic and gravitational radiation travel differently.
In modified gravity, dark matter is not made of particles. Instead, the gravitational pull felt by normal matter comes from a gravitational potential that is not the one predicted by general relativity. In general relativity and its modifications likewise, the gravitational potential is described by the curvature of space-time and encoded in what is called the “metric.” In the versions of modified gravity studied in the new paper, the metric has additional terms which effectively act on normal matter as if there was dark matter, even though there is no dark matter.
However, the metric in general relativity is also what gives rise to gravitational waves, which are small, periodic disturbances of that metric. If dark matter is made of particles, then the gravitational waves themselves travel through the gravitational potential of normal plus dark matter. If dark matter, however, is due to a modification of the gravitational potential, then gravitational waves themselves do not feel the dark matter potential.
This can be probed if you send both types of signals, electromagnetic and gravitational, through a gravitational potential, for example that of the Milky Way. The presence of the gravitational potential increases the run-time of the signal, and the deeper the potential, the longer the run-time. This is known as “Shapiro-delay” and is one of the ways, for example, to probe general relativity in the solar system.
The authors of the paper put in the numbers and find that the difference between the potential with dark matter for electromagnetic radiation and the potential without dark matter for gravitational radiation adds up to about a year for the Milky Way alone. On top come some hundred days more delay if you also take into account galaxies that the signals passed by on the way from the source to Earth. If correct, this means that the almost simultaneous arrival of both signals rules out the modifications of gravity which lead to differences in the travel-time by many orders of magnitude.
The logic of the argument is this. We know that galaxies cause gravitational lensing as if they contain dark matter. This means even if dark matter can be ascribed to modified gravity, its effect on light must be like that of dark matter. The Shapiro-delay isn’t exactly the same as gravitational lensing, but the origin of both effects is mathematically similar. This makes it plausible that the Shapiro-delay for electromagnetic radiation scales with the dark matter mass, regardless of its origin. The authors assume that the delay for the gravitational waves in modified gravity is just due to normal matter. This means that gravitational waves should arrive much sooner than their electromagnetic company because the potential the gravitational waves feel is much shallower.
The Shapiro-delay on the Sun is about 10^{-4} seconds. If you scale this up to the Milky Way, with a mass of about 10^{12} times that of the Sun, this gives 10^{8} seconds, which is indeed about a year or so. You gain a little since the dark matter mass is somewhat higher and lose a little because the Milky Way isn’t spherically symmetric. But by order of magnitude this simple estimate explains the constraint.
The paper hence rules out all modified gravity theories that predict gravitational waves which pass differently through the gravitational potential of galaxies than electromagenetic waves do. This does not affect all types of modified gravity, but it does affect, according to the paper, Bekenstein’s TeVeS and Moffat’s Scalar-Vector-Tensor theory.
A word of caution, however, is that the paper does not contain, and I have not seen, an actual calculation for the delay of gravitational waves in the respective modified gravity models. Though the estimate seems good, it’s sketchy on the math.
I think the paper is a big step forward. I am not sold on either modified gravity or particle dark matter and think both have their pros and cons. To me, particle dark matter seems plausible and it works well on all scales, while modified gravity doesn’t work so well on cosmological (super-galactic) scales. On the other hand, we haven’t directly measured any dark matter particles, and some of the observed regularities in galaxies are not well explained by the particle-hypothesis.
But as wonderful as it is to cross some models off the list, ruling out certain types of modified gravity doesn’t make particle dark matter any better. The reason you never hear anyone claim that particle dark matter has been ruled out is that it’s not possible to rule it out. The idea is so flexible and the galactic simulations have so many parameters you can explain everything.
This is why I have lately been intrigued by the idea that dark matter is a kind of superfluid which, in certain approximations, behaves like modified gravity. This can explain the observed regularities while maintaining the benefits of particle dark matter. For all I can tell, the new constraint doesn’t apply to this type of superfluid (one of the authors of the new paper confirmed this to me).
In summary, let me emphasize that this new observation doesn’t rule out modified gravity any more than the no-detection of Weakly Interacting Massive Particles rules out particle dark matter. So please don’t jump to conclusions. It rules out certain types of modified gravity, no more and no less. But this paper gives me hope that a resolution of the dark matter mystery might happen in my lifetime.
- GW170817 Falsifies Dark Matter Emulators
Sibel Boran, Shantanu Desai, Emre Kahya, Richard Woodard
arXiv:1710.06168 [astro-ph.HE]
The observation is difficult to explain with some variants of modified gravity because in these models electromagnetic and gravitational radiation travel differently.
In modified gravity, dark matter is not made of particles. Instead, the gravitational pull felt by normal matter comes from a gravitational potential that is not the one predicted by general relativity. In general relativity and its modifications likewise, the gravitational potential is described by the curvature of space-time and encoded in what is called the “metric.” In the versions of modified gravity studied in the new paper, the metric has additional terms which effectively act on normal matter as if there was dark matter, even though there is no dark matter.
However, the metric in general relativity is also what gives rise to gravitational waves, which are small, periodic disturbances of that metric. If dark matter is made of particles, then the gravitational waves themselves travel through the gravitational potential of normal plus dark matter. If dark matter, however, is due to a modification of the gravitational potential, then gravitational waves themselves do not feel the dark matter potential.
This can be probed if you send both types of signals, electromagnetic and gravitational, through a gravitational potential, for example that of the Milky Way. The presence of the gravitational potential increases the run-time of the signal, and the deeper the potential, the longer the run-time. This is known as “Shapiro-delay” and is one of the ways, for example, to probe general relativity in the solar system.
The authors of the paper put in the numbers and find that the difference between the potential with dark matter for electromagnetic radiation and the potential without dark matter for gravitational radiation adds up to about a year for the Milky Way alone. On top come some hundred days more delay if you also take into account galaxies that the signals passed by on the way from the source to Earth. If correct, this means that the almost simultaneous arrival of both signals rules out the modifications of gravity which lead to differences in the travel-time by many orders of magnitude.
The logic of the argument is this. We know that galaxies cause gravitational lensing as if they contain dark matter. This means even if dark matter can be ascribed to modified gravity, its effect on light must be like that of dark matter. The Shapiro-delay isn’t exactly the same as gravitational lensing, but the origin of both effects is mathematically similar. This makes it plausible that the Shapiro-delay for electromagnetic radiation scales with the dark matter mass, regardless of its origin. The authors assume that the delay for the gravitational waves in modified gravity is just due to normal matter. This means that gravitational waves should arrive much sooner than their electromagnetic company because the potential the gravitational waves feel is much shallower.
The Shapiro-delay on the Sun is about 10^{-4} seconds. If you scale this up to the Milky Way, with a mass of about 10^{12} times that of the Sun, this gives 10^{8} seconds, which is indeed about a year or so. You gain a little since the dark matter mass is somewhat higher and lose a little because the Milky Way isn’t spherically symmetric. But by order of magnitude this simple estimate explains the constraint.
The paper hence rules out all modified gravity theories that predict gravitational waves which pass differently through the gravitational potential of galaxies than electromagenetic waves do. This does not affect all types of modified gravity, but it does affect, according to the paper, Bekenstein’s TeVeS and Moffat’s Scalar-Vector-Tensor theory.
A word of caution, however, is that the paper does not contain, and I have not seen, an actual calculation for the delay of gravitational waves in the respective modified gravity models. Though the estimate seems good, it’s sketchy on the math.
I think the paper is a big step forward. I am not sold on either modified gravity or particle dark matter and think both have their pros and cons. To me, particle dark matter seems plausible and it works well on all scales, while modified gravity doesn’t work so well on cosmological (super-galactic) scales. On the other hand, we haven’t directly measured any dark matter particles, and some of the observed regularities in galaxies are not well explained by the particle-hypothesis.
But as wonderful as it is to cross some models off the list, ruling out certain types of modified gravity doesn’t make particle dark matter any better. The reason you never hear anyone claim that particle dark matter has been ruled out is that it’s not possible to rule it out. The idea is so flexible and the galactic simulations have so many parameters you can explain everything.
This is why I have lately been intrigued by the idea that dark matter is a kind of superfluid which, in certain approximations, behaves like modified gravity. This can explain the observed regularities while maintaining the benefits of particle dark matter. For all I can tell, the new constraint doesn’t apply to this type of superfluid (one of the authors of the new paper confirmed this to me).
In summary, let me emphasize that this new observation doesn’t rule out modified gravity any more than the no-detection of Weakly Interacting Massive Particles rules out particle dark matter. So please don’t jump to conclusions. It rules out certain types of modified gravity, no more and no less. But this paper gives me hope that a resolution of the dark matter mystery might happen in my lifetime.
Friday, October 20, 2017
Space may not be as immaterial as we thought
Galaxy slime. [Img Src] |
We shouldn’t speak of space and time as if the two were distant cousins. We have known at least since Einstein that space and time are inseparable, two hemispheres of the same cosmic brain, joined to a single entity: space-time. Einstein also taught us that space-time isn’t flat, like a paper, but bent and wiggly, like a rubber sheet. Space-time curves around mass and energy, and this gives rise to the effect we call gravity.
That’s what Einstein said. But turns out if you write down the equations for small wiggles in a medium – such as soundwaves in a fluid – then the equations look exactly like those of waves in a curved background.
Yes, that’s right. Sometimes, waves in fluids behave like waves in a curved space-time; they behave like waves in a gravitational field. Fluids, therefore, can be used to simulate gravity. And that’s some awesome news because this correspondence between fluids and gravity allows physicists to study situations that are otherwise experimentally inaccessible, for example what happens near a black hole horizon, or during the rapid expansion in the early universe.
This mathematical relation between fluids and gravity is known as “analog gravity.” That’s “analog” as in “analogy” not as opposed to digital. But it’s not just math. The first gravitational analogies have meanwhile been created in a laboratory.
Most amazing is the work by Jeff Steinhauer at Technion, Israel. Steinhauer used a condensate of supercooled atoms that “flows” in a potential of laser beams which simulate the black hole horizon. In his experiment, Steinhauer wanted to test whether black holes emit radiation as Stephen Hawking predicted. The temperature of real, astrophysical, black holes is too small to be measurable. But if Hawking’s calculation is right, then the fluid-analogy of black holes should radiate too.
Black holes trap light behind the “event horizon.” A fluid that simulates a black hole doesn’t trap light, it traps instead the fluid’s soundwaves behind what is called the “acoustic horizon.” Since the fluid analogies of black holes aren’t actually black, Bill Unruh suggested to call them “dumb holes.” The name stuck.
But whether the horizon catches light or sound, Hawking-radiation should be produced regardless, and it should appear in form of fluctuations (in the fluid or quantum matter fields, respectively) that are paired across the horizon.
Steinhauer claims he has measured Hawking-radiation produced by an acoustic black hole. His results are presently somewhat controversial – not everyone is convinced he has really measured what he claims he did – but I am sure sooner or later this will be settled. More interesting is that Steinhauer’s experiment showcases the potential of the method.
Of course fluid-analogies are still different from real gravity. Mathematically the most important difference is that the curved space-time which the fluid mimics has to be designed. It is not, as for real gravity, an automatic reaction to energy and matter; instead, it is part of the experimental setup. However, this is a problem which at least in principle can be overcome with a suitable feedback loop.
The conceptually more revealing difference is that the fluid’s correspondence to a curved space-time breaks down once the experiment starts to resolve the fluid’s atomic structure. Fluids, we know, are made of smaller things. Curved space-time, for all we presently know, isn’t. But how certain are we of this? What if the fluid analogy is more than an analogy? Maybe space-time really behaves like a fluid; maybe it is a fluid. And if so, the experiments with fluid-analogies may reveal how we can find evidence for a substructure of space-time.
Some have pushed the gravity-fluid analogy even further. Gia Dvali from LMU Munich, for example, has proposed that real black holes are condensates of gravitons, the hypothetical quanta of the gravitational field. This simple idea, he claims, explains several features of black holes which have so-far puzzled physicists, notably the question how black holes manage to keep the information that falls into them.
We used to think black holes are almost featureless round spheres. But if they are instead, as Dvali says, condensates of many gravitons, then black holes can take on many slightly different configuration in which information can be stored. Even more interesting, Dvali proposes the analogy could be used to design fluids which are as efficient at storing and distributing information as black holes are. The link between condensed matter and astrophysics, hence, works both ways.
Physicists have looked for evidence of space-time being a medium for some while. For example by studying light from distant sources, such as gamma-ray bursts, they tried to find out whether space has viscosity or whether it causes dispersion (a running apart of frequencies like in a prism). A new line of research is to search for impurities – “space-time defects” – like crystals have them. So far the results have been negative. But the experiments with fluid analogies might point the way forward.
If space-time is made of smaller things, this could solve a major problem: How to describe the quantum behavior of space time. Unlike all the other interactions we know of, gravity is a non-quantum theory. This means it doesn’t fit together with the quantum theories that physicists use for elementary particles. All attempts to quantize gravity so-far have either failed or remained unconfirmed speculations. That space itself isn’t fundamental but made of other things is one way to approach the problem.
Not everyone likes the idea. What irks physicists most about giving substance to space-time is that this breaks Einstein’s bond between space and time which has worked dramatically well – so far. Only further experiment will reveal whether Einstein’s theory holds up.
Time flows, they say. Maybe space does too.
This article previously appeared on iai.news.
Tuesday, October 17, 2017
I totally mean it: Inflation never solved the flatness problem.
I’ve had many interesting reactions to my recent post about inflation, this idea that the early universe expanded exponentially and thereby flattened and smoothed itself. The maybe most interesting response to my pointing out that inflation doesn’t solve the problems it was invented to solve is a flabbergasted: “But everyone else says it does.”
Not like I don’t know that. But, yes, most people who work on inflation don’t even get the basics right.
I’m not sure why that is so. Those who I personally speak with pretty quickly agree that what I say is correct. The math isn’t all that difficult and the situation pretty clar. The puzzle is, why then do so many of them tell a story that is nonsense? And why do they keep teaching it to students, print it in textbooks, and repeat it in popular science books?
I am fascinated by this for the same reason I’m fascinated by the widely-spread and yet utterly wrong idea that the Bullet-cluster rules out modified gravity. As I explained in an earlier blogpost, it doesn’t. Never did. The Bullet-cluster can be explained just fine with modified gravity. It’s difficult to explain with particle dark matter. But, eh, just the other day I met a postdoc who told me the Bullet-cluster rules out modified gravity. Did he ever look at the literature? No.
One reason these stories survive – despite my best efforts to the contrary – is certainly that they are simple and sound superficially plausible. But it doesn’t take much to tear them down. And that it’s so simple to pull away the carpet under what motivates research of thousands of people makes me very distrustful of my colleagues.
Let us return to the claim that inflation solves the flatness problem. Concretely, the problem is that in cosmology there’s a dynamical variable (ie, one that depends on time), called the curvature density parameter. It’s by construction dimensionless (doesn’t have units) and its value today is smaller than 0.1 or so. The exact digits don’t matter all that much.
What’s important is that this variable increases in value over time, meaning it must have been smaller in the past. Indeed, if you roll it back to the Planck epoch or so, it must have been something like 10^{-60}, take or give some orders of magnitude. That’s what they call the flatness problem.
Now you may wonder, what’s problematic about this. How is it surprising that the value of something which increases in time was smaller in the past? It’s an initial value that’s constrained by observation and that’s really all there is to say about it.
It’s here where things get interesting: The reason that cosmologists believe it’s a problem is that they think a likely value for the curvature density at early times should have been close to 1. Not exactly one, but not much smaller and not much larger. Why? I have no idea.
Each time I explain this obsession with numbers close to 1 to someone who is not a physicist, they stare at me like I just showed off my tin foil hat. But, yeah, that’s what they preach down here. Numbers close to 1 are good. Small or large numbers are bad. Therefore, cosmologists and high-energy physicists believe that numbers close to 1 are more likely initial conditions. It’s like a bizarre cult that you’re not allowed to question.
But if you take away one thing from this blogpost it’s that whenever someone talks about likelihood or probability you should ask “What’s the probability distribution and where does it come from?”
The probability distribution is what you need to define just how likely each possible outcome is. For a fair dice, for example, it’s 1/6 for each outcome. For a not-so-fair dice it could be any combination of numbers, so long as the probabilities all add to 1. There are infinitely many probability distributions and without defining one it is not clear what “likely” means.
If you ask physicists, you will quickly notice that neither for inflation nor for theories beyond the standard model does anyone have a probability distribution or ever even mentions a probability distribution for the supposedly likely values.
How does it matter?
The theories that we currently have work with differential equations and inflation is no exception. But the systems that we observe are not described by the differential equations themselves, they are described by solutions to the equation. To select the right solution, we need an initial condition (or several, depending on the type of equation). You know the drill from Newton’s law: You have an equation, but you only can tell where the arrow will fly if you also know the arrow’s starting position and velocity.
The initial conditions are either designed by the experimenter or inferred from observation. Either way, they’re not predictions. They can not be predicted. That would be a logical absurdity. You can’t use a differential equation to predict its own initial conditions. If you want to speak about the probability of initial conditions you need another theory.
What happens if you ignore this and go with the belief that the likely initial value for the curvature density should be about 1? Well, then you do have a problem indeed, because that’s incompatible with data to a high level of significance.
Inflation then “solves” this supposed problem by taking the initial value and shrinking it by, I dunno, 100 or so orders of magnitude. This has the consequence that if you start with something of order 1 and add inflation, the result today is compatible with observation. But of course if you start with some very large value, say 10^{60}, then the result will still be incompatible with data. That is, you really need the assumption that the initial values are likely to be of order 1. Or, to put it differently, you are not allowed to ask why the initial value was not larger than some other number.
This fineprint, that there are still initial values incompatible with data, often gets lost. A typical example is what Jim Baggot writes in his book “Origins” about inflation:
But it’s unfair to pick on Jim because this oversimplification is so common. Ethan Siegel, for example, is another offender. He writes:
You might say then, but doesn’t inflation at least greatly improve the situation? Isn’t it better because it explains there are more values compatible with observation? No. Because you have to pay a price for this “explanation:” You have to introduce a new field and a potential for that field and then a way to get rid of this field once it’s done its duty.
I am pretty sure if you’d make a Bayesian estimate to quantify the complexity of these assumptions, then inflation would turn out to be more complicated than just picking some initial parameter. Is there really any simpler assumption than just some number?
Some people have accused me of not understanding that science is about explaining things. But I do not say we should not try to find better explanations. I say that inflation is not a better explanation for the present almost-flatness of the universe than just saying the initial value was small.
Shrinking the value of some number by pulling exponential factors out of thin air is not a particularly impressive gimmick. And if you invent exponential factors already, why not put them into the probability distribution instead?
Let me give you an example for why the distinction matters. Suppose you just hatched from an egg and don’t know anything about astrophysics. You brush off a loose feather and look at our solar system for the first time. You notice immediately that the planetary orbits almost lie in the same plane.
Now, if you assume a uniform probability distribution for the initial values of the orbits, that’s an incredibly unlikely thing to happen. You would think, well, that needs explaining. Wouldn’t you?
The inflationary approach to solving this problem would be to say the orbits started with random values but then some so-far unobserved field pulled them all into the same plane. Then the field decayed so we can’t measure it. “Problem solved!” you yell and wait for the Nobel Prize.
But the right explanation is that due to the way the solar system formed, the initial values are likely to lie in a plane to begin with! You got the initial probability distribution wrong. There’s no fancy new field.
In the case of the solar system you could learn to distinguish dynamics from initial conditions by observing more solar systems. You’d find that aligned orbits are the rule not the exception. You’d then conclude that you should look for a mechanism that explains the initial probability distribution and not a dynamical mechanism to change the uniform distribution later.
In the case of inflation, unfortunately, we can’t do such an observation since this would require measuring the initial value of the curvature density in other universes.
While I am at it, it’s interesting to note that the erroneous argument against the heliocentric solar system, that the stars would have to be “unnaturally” far away, was based on the same mistake that the just-hatched chick made. Astronomers back then implicitly assumed a probability distribution for distances between stellar objects that was just wrong. (And, yes, I know they also wrongly estimated the size of the stars.)
In the hope that you’re still with me, let me emphasize that nevertheless I think inflation is a good theory. Even though it does not solve the flatness problem (or monopole problem or horizon problem) it explains certain correlations in the cosmic-microwave-background. (ET anticorrelations for certain scales, shown in the figure below.)
In the case of these correlations, adding inflation greatly simplifies the initial condition that gives rise to the observation. I am not aware that someone actually has quantified this simplification but I’m sure it could be done (and it should be done). Therefore, inflation actually is the better explanation. For the curvature, however, that isn’t so because replacing one number with another number times some exponential factor doesn’t explain anything.
I hope that suffices to convince you that it’s not me who is nuts.
I have a lot of sympathy for the need to sometimes oversimplify scientific explanations to make them accessible to non-experts. I really do. But the narrative that inflation solves the flatness problem can be found even in papers and textbooks. In fact, you can find it in the above-mentioned lecture notes! It’s about time this myth vanishes from the academic literature.
Not like I don’t know that. But, yes, most people who work on inflation don’t even get the basics right.
Inflation flattens the universe like photoshop flattens wrinkles. Impressive! [Img Src] |
I’m not sure why that is so. Those who I personally speak with pretty quickly agree that what I say is correct. The math isn’t all that difficult and the situation pretty clar. The puzzle is, why then do so many of them tell a story that is nonsense? And why do they keep teaching it to students, print it in textbooks, and repeat it in popular science books?
I am fascinated by this for the same reason I’m fascinated by the widely-spread and yet utterly wrong idea that the Bullet-cluster rules out modified gravity. As I explained in an earlier blogpost, it doesn’t. Never did. The Bullet-cluster can be explained just fine with modified gravity. It’s difficult to explain with particle dark matter. But, eh, just the other day I met a postdoc who told me the Bullet-cluster rules out modified gravity. Did he ever look at the literature? No.
One reason these stories survive – despite my best efforts to the contrary – is certainly that they are simple and sound superficially plausible. But it doesn’t take much to tear them down. And that it’s so simple to pull away the carpet under what motivates research of thousands of people makes me very distrustful of my colleagues.
Let us return to the claim that inflation solves the flatness problem. Concretely, the problem is that in cosmology there’s a dynamical variable (ie, one that depends on time), called the curvature density parameter. It’s by construction dimensionless (doesn’t have units) and its value today is smaller than 0.1 or so. The exact digits don’t matter all that much.
What’s important is that this variable increases in value over time, meaning it must have been smaller in the past. Indeed, if you roll it back to the Planck epoch or so, it must have been something like 10^{-60}, take or give some orders of magnitude. That’s what they call the flatness problem.
Now you may wonder, what’s problematic about this. How is it surprising that the value of something which increases in time was smaller in the past? It’s an initial value that’s constrained by observation and that’s really all there is to say about it.
It’s here where things get interesting: The reason that cosmologists believe it’s a problem is that they think a likely value for the curvature density at early times should have been close to 1. Not exactly one, but not much smaller and not much larger. Why? I have no idea.
Each time I explain this obsession with numbers close to 1 to someone who is not a physicist, they stare at me like I just showed off my tin foil hat. But, yeah, that’s what they preach down here. Numbers close to 1 are good. Small or large numbers are bad. Therefore, cosmologists and high-energy physicists believe that numbers close to 1 are more likely initial conditions. It’s like a bizarre cult that you’re not allowed to question.
But if you take away one thing from this blogpost it’s that whenever someone talks about likelihood or probability you should ask “What’s the probability distribution and where does it come from?”
The probability distribution is what you need to define just how likely each possible outcome is. For a fair dice, for example, it’s 1/6 for each outcome. For a not-so-fair dice it could be any combination of numbers, so long as the probabilities all add to 1. There are infinitely many probability distributions and without defining one it is not clear what “likely” means.
If you ask physicists, you will quickly notice that neither for inflation nor for theories beyond the standard model does anyone have a probability distribution or ever even mentions a probability distribution for the supposedly likely values.
How does it matter?
The theories that we currently have work with differential equations and inflation is no exception. But the systems that we observe are not described by the differential equations themselves, they are described by solutions to the equation. To select the right solution, we need an initial condition (or several, depending on the type of equation). You know the drill from Newton’s law: You have an equation, but you only can tell where the arrow will fly if you also know the arrow’s starting position and velocity.
The initial conditions are either designed by the experimenter or inferred from observation. Either way, they’re not predictions. They can not be predicted. That would be a logical absurdity. You can’t use a differential equation to predict its own initial conditions. If you want to speak about the probability of initial conditions you need another theory.
What happens if you ignore this and go with the belief that the likely initial value for the curvature density should be about 1? Well, then you do have a problem indeed, because that’s incompatible with data to a high level of significance.
Inflation then “solves” this supposed problem by taking the initial value and shrinking it by, I dunno, 100 or so orders of magnitude. This has the consequence that if you start with something of order 1 and add inflation, the result today is compatible with observation. But of course if you start with some very large value, say 10^{60}, then the result will still be incompatible with data. That is, you really need the assumption that the initial values are likely to be of order 1. Or, to put it differently, you are not allowed to ask why the initial value was not larger than some other number.
This fineprint, that there are still initial values incompatible with data, often gets lost. A typical example is what Jim Baggot writes in his book “Origins” about inflation:
“when inflation was done, flat spacetime was the only result.”Well, that’s wrong. I checked with Jim and he totally knows the math. It’s not like he doesn’t understand it. He just oversimplifies it maybe a little too much.
But it’s unfair to pick on Jim because this oversimplification is so common. Ethan Siegel, for example, is another offender. He writes:
“if the Universe had any intrinsic curvature to it, it was stretched by inflation to be indistinguishable from “flat” today.”That’s wrong too. It is not the case for “any” intrinsic curvature that the outcome will be almost flat. It’s correct only for initial values smaller than something. He too, after some back and forth, agreed with me. Will he change his narrative? We will see.
You might say then, but doesn’t inflation at least greatly improve the situation? Isn’t it better because it explains there are more values compatible with observation? No. Because you have to pay a price for this “explanation:” You have to introduce a new field and a potential for that field and then a way to get rid of this field once it’s done its duty.
I am pretty sure if you’d make a Bayesian estimate to quantify the complexity of these assumptions, then inflation would turn out to be more complicated than just picking some initial parameter. Is there really any simpler assumption than just some number?
Some people have accused me of not understanding that science is about explaining things. But I do not say we should not try to find better explanations. I say that inflation is not a better explanation for the present almost-flatness of the universe than just saying the initial value was small.
Shrinking the value of some number by pulling exponential factors out of thin air is not a particularly impressive gimmick. And if you invent exponential factors already, why not put them into the probability distribution instead?
Let me give you an example for why the distinction matters. Suppose you just hatched from an egg and don’t know anything about astrophysics. You brush off a loose feather and look at our solar system for the first time. You notice immediately that the planetary orbits almost lie in the same plane.
Now, if you assume a uniform probability distribution for the initial values of the orbits, that’s an incredibly unlikely thing to happen. You would think, well, that needs explaining. Wouldn’t you?
The inflationary approach to solving this problem would be to say the orbits started with random values but then some so-far unobserved field pulled them all into the same plane. Then the field decayed so we can’t measure it. “Problem solved!” you yell and wait for the Nobel Prize.
But the right explanation is that due to the way the solar system formed, the initial values are likely to lie in a plane to begin with! You got the initial probability distribution wrong. There’s no fancy new field.
In the case of the solar system you could learn to distinguish dynamics from initial conditions by observing more solar systems. You’d find that aligned orbits are the rule not the exception. You’d then conclude that you should look for a mechanism that explains the initial probability distribution and not a dynamical mechanism to change the uniform distribution later.
In the case of inflation, unfortunately, we can’t do such an observation since this would require measuring the initial value of the curvature density in other universes.
While I am at it, it’s interesting to note that the erroneous argument against the heliocentric solar system, that the stars would have to be “unnaturally” far away, was based on the same mistake that the just-hatched chick made. Astronomers back then implicitly assumed a probability distribution for distances between stellar objects that was just wrong. (And, yes, I know they also wrongly estimated the size of the stars.)
In the hope that you’re still with me, let me emphasize that nevertheless I think inflation is a good theory. Even though it does not solve the flatness problem (or monopole problem or horizon problem) it explains certain correlations in the cosmic-microwave-background. (ET anticorrelations for certain scales, shown in the figure below.)
Figure 3.9 from Daniel Baumann’s highly recommendable lecture notes. |
In the case of these correlations, adding inflation greatly simplifies the initial condition that gives rise to the observation. I am not aware that someone actually has quantified this simplification but I’m sure it could be done (and it should be done). Therefore, inflation actually is the better explanation. For the curvature, however, that isn’t so because replacing one number with another number times some exponential factor doesn’t explain anything.
I hope that suffices to convince you that it’s not me who is nuts.
I have a lot of sympathy for the need to sometimes oversimplify scientific explanations to make them accessible to non-experts. I really do. But the narrative that inflation solves the flatness problem can be found even in papers and textbooks. In fact, you can find it in the above-mentioned lecture notes! It’s about time this myth vanishes from the academic literature.
Friday, October 13, 2017
Is the inflationary universe a scientific theory? Not anymore.
Living in a Bubble? [Image: YouTube] |
Inflation was proposed more than 35 years ago, among others, by Paul Steinhardt. But Steinhardt has become one of the theory’s most fervent critics. In a recent article in Scientific American, Steinhardt together with Anna Ijjas and Avi Loeb, don’t hold back. Most cosmologists, they claim, are uncritical believers:
“[T]he cosmology community has not taken a cold, honest look at the big bang inflationary theory or paid significant attention to critics who question whether inflation happened. Rather cosmologists appear to accept at face value the proponents’ assertion that we must believe the inflationary theory because it offers the only simple explanation of the observed features of the universe.”And it's even worse, they argue, inflation is not even a scientific theory:
“[I]nflationary cosmology, as we currently understand it, cannot be evaluated using the scientific method.”As alternative to inflation, Steinhardt et al promote a “big bounce” in which the universe’s expansion was preceded by a phase of contraction, yielding similar benefits to inflation.
The group’s fight against inflation isn’t news. They laid out their arguments in a series of papers during the last years (on which I previously commented here). But the recent SciAm piece called The Defenders Of Inflation onto stage. Lead by David Kaiser, they signed a letter to Scientific American in which they complained that the magazine gave space to the inflationary criticism.
The letter’s list of undersigned is an odd selection of researchers who themselves work on inflation and of physics luminaries who have little if anything to do with inflation. Interestingly, Slava Mukhanov – one of the first to derive predictions from inflation – did not sign. And it’s not because he wasn’t asked. In an energetic talk delivered at Stephen Hawking’s birthday conference two months ago, Mukhanov made it pretty clear that he thinks most of the inflationary model building is but a waste of time.
I agree with Muhkanov’s assessment. The Steinhardt et al article isn’t exactly a masterwork of science writing. It’s also unfortunate they’re using SciAm to promote some other theory of how the universe began rather than sticking to their criticism of inflation. But some criticism is overdue.
The problem with inflation isn’t the idea per se, but the overproduction of useless inflationary models. There are literally hundreds of these models, and they are – as the philosophers say – severely underdetermined. This means if one extrapolates any models that fits current data to a regime which is still untested, the result is ambiguous. Different models lead to very different predictions for not-yet made observations. Presently, is therefore utterly pointless to twiddle with the details of inflation because there are literally infinitely many models one can think up.
Rather than taking on this overproduction problem, however, Steinhardt et al in their SciAm piece focus on inflation’s failure to solve the problems it was meant to solve. But that’s an idiotic criticism because the problems that inflation was meant to solve aren’t problems to begin with. I’m serious. Let’s look at those one by one:
1. The Monopole Problem
Guth invented inflation to solve the “monopole problem.” If the early universe underwent a phase-transition, for example because the symmetry of grand unification was broken – then topological defects, like monopoles, should have been produced abundantly. We do not, however, see any of them. Inflation dilutes the density of monopoles (and other worries) so that it’s unlikely we’ll ever encounter one.
But a plausible explanation for why we don’t see any monopoles is that there aren’t any. We don’t know there is any grand symmetry that was broken in the early universe, or if there is, we don’t know when it was broken, or if the breaking produced any defects. Indeed, all searchers for evidence of grand symmetry – mostly via proton decay – turned out negative. This motivation is interesting today merely for historical reasons.
2. The Flatness Problem
The flatness problem is a finetuning problem. The universe currently seems to be almost flat, or if it has curvature, then that curvature must be very small. The contribution of curvature to the dynamics of the universe however increases in relevance relative to that of matter. This means if the curvature density parameter is small today, it must have been even smaller in the past. Inflation serves to make any initial curvature contribution smaller by something like 100 orders of magnitude or so.
This is supposed to be an explanation, but it doesn’t explain anything, for now you can ask, well, why wasn’t the original curvature larger than some other number? The reason that some physicists believe something is being explained here is that numbers close to 1 are pretty according to current beauty-standards, while numbers much smaller than 1 numbers aren’t. The flatness problem, therefore, is an aesthetic problem, and I don’t think it’s an argument any scientist should take seriously.
3. The Horizon Problem
The Cosmic Microwave Background (CMB) has almost at the same temperature in all directions. Problem is, if you trace back the origin the background radiation without inflation, then you find that the radiation that reached us from different directions was never in causal contact with each other. Why then does it have the same temperature in all directions?
To see why this problem isn’t a problem, you have to know how the theories that we currently use in physics work. We have an equation – a “differential equation” – that tells us how a system (eg, the universe) changes from one place to another and one moment to another. To make any use of this equation, however, we also need starting values or “initial conditions.”*
The horizon problem asks “why this initial condition” for the universe. This question is justified if an initial condition is complicated in the sense of requiring a lot of information. But a homogeneous temperature isn’t complicated. It’s dramatically easy. And not only isn’t there much to explain, inflation moreover doesn’t even answer the question “why this initial condition” because it still needs an initial condition. It’s just a different initial condition. It’s not any simpler and it doesn’t explain anything.
Another way to see that this is a non-problem: If you’d go back in time far enough without inflation, you’d eventually get to a period when matter was so dense and curvature so high that quantum gravity was important. And what do we know about the likelihood of initial conditions in a theory of quantum gravity? Nothing. Absolutely nothing.
That we’d need quantum gravity to explain the initial condition for the universe, however, is an exceedingly unpopular point of view because nothing can be calculated and no predictions can be made.
Inflation, on the other hand, is a wonderfully productive model that allows cosmologists to churn out papers.
You will find the above three problems religiously repeated as a motivation for inflation, in lectures and textbooks and popular science pages all over the place. But these problems aren’t problems, never were problems, and never required a solution.
Even though inflation was ill-motivated when conceived, however, it later turned out to actually solve some real problems. Yes, sometimes physicists work on the wrong things for the right reasons, and sometimes they work on the right things for the wrong reasons. Inflation is an example for the latter.
The reasons why many physicists today think something like inflation must have happened are not that it supposedly solve the three above problems. It’s that some features of the CMB have correlations (the “TE power spectrum”) which depend on the size of the fluctuations, and implies a dependence on the size of the universe. This correlation, therefore, cannot be easily explained by just choosing an initial condition, since it is data that goes back to different times. It really tells us something about how the universe changed with time, not just where it started from.**
Two more convincing features of inflation are that, under fairly general circumstances, the model also explains the absence of certain correlations in the CMB (the “non-Gaussianities”) and how many CMB fluctuations there are of any size, quantified by what is known as the “scale factor.”
But here is the rub. To make predictions with inflation one cannot just say “there once was exponential expansion and it ended somehow.” No, to be able to calculate something, one needs a mathematical model. The current models for inflation work by introducing a new field – the “inflaton” – and give this field a potential energy. The potential energy depends on various parameters. And these parameters can then be related to observations.
The scientific approach to the situation would be to choose a model, determine the parameters that best fit observations, and then revise the model as necessary – ie, as new data comes in. But that’s not what cosmologists presently do. Instead, they have produced so many variants of models that they can now “predict” pretty much anything that might be measured in the foreseeable future.
It is this abundance of useless models that gives rise to the criticism that inflation is not a scientific theory. And on that account, the criticism is justified. It’s not good scientific practice. It is a practice that, to say it bluntly, has become commonplace because it results in papers, not because it advances science.
I was therefore dismayed to see that the criticism by Steinhardt, Ijas, and Loeb was dismissed so quickly by a community which has become too comfortable with itself. Inflation is useful because it relates existing observations to an underlying mathematical model, yes. But we don’t yet have enough data to make reliable predictions from it. We don’t even have enough data to convincingly rule out alternatives.
There hasn’t been a Nobelprize for inflation, and I think the Nobel committee did well in that decision.
There’s no warning sign you when you cross the border between science and blabla-land. But inflationary model building left behind reasonable scientific speculation long ago. I, for one, am glad that at least some people are speaking out about it. And that’s why I approve of the Steinhardt et al criticism.
* Contrary to what the name suggest, the initial conditions could be at any moment, not necessarily the initial one. We would still call them initial conditions.
** This argument is somewhat circular because extracting the time-dependence for the modes already presumes something like inflation. But at least it’s a strong indicator.
This article was previously published on Starts With A Bang.
Wednesday, October 11, 2017
Tuesday, October 03, 2017
Yet another year in which you haven’t won a Nobel Prize!
“Do you hope to win a Nobel Prize?” asked an elderly man who had come to shake my hand after the lecture. I laughed, but he was serious. Maybe I had been a little too successful explaining how important quantum gravity is.
No, I don’t hope to win a Nobel Prize. If that’s what I’d been after, I certainly would have chosen a different field. Condensed matter physics, say, or quantum things. At least cosmology. But certainly not quantum gravity.
But the Nobel Prize is important for science. It’s important not because it singles out a few winners but because in science it’s the one annual event that catches everybody’s attention. On which other day does physics make headlines?
In recent years I heard increasingly louder calls that the Prize-criteria should be amended so that more than three people can win. I am not in favor of that. It doesn’t make sense anyway to hand out exactly one Prize each year regardless of how much progress was made. There is always a long list of people who deserved a Nobel but never got one. Like Vera Rubin, who died last year and who by every reasonable measure should have gotten one. Shame on you, Nobel Committee.
I am particularly opposed to the idea that the Nobel Prize should be awarded to collaborations with members sometimes in the hundreds or even thousands. While the three-people-cutoff is arguably arbitrary, I am not in favor of showering collaboration members with fractional prizes. Things don’t get going because a thousand scientists spontaneously decide to make an experiment. It’s always but a few people who are responsible to make things happen. Those are the ones which the Nobel committee should identify.
So, I am all in favor of the Nobel Prize and like it the way it is. But (leaving aside that many institutions seem to believe Nobel Prize winners lay golden eggs) the Prize has little relevance in research. I definitely know a few people who hope to win it and some even deserve it. But I yet have to meet anyone who deliberately chose their research with that goal in mind.
The Nobel Prize is by construction meant to honor living scientists. This makes sense because otherwise we’d have a backlog of thousands of deceased scientific luminaries and nobody would be interested watching the announcement. But in some research areas we don’t expect to see payoffs in our lifetime. Quantum gravity is one of them.
Personally, I feel less inspired by Nobel Prize winners than by long-dead geniuses like Da Vinci, Leibnitz, or Goethe – masterminds whose intellectual curiosity spanned disciplines. They were ahead of their time and produced writings that not rarely were vague, hard to follow, and sometimes outright wrong. None of them would have won a Nobel Prize had the Prize existed at the time. But their insights laid the basis for centuries of scientific progress.
And so, while we honor those who succeed in the present, let’s not forget that somewhere among us, unrecognized, are the seeds that will grow to next centuries’ discoveries.
Today, as the 2017 Nobel prize is awarded, I want to remind those of you who work in obscure research areas, produce unpopular artworks, or face ridicule for untimely writing, that history will be your final judge, not your contemporaries.
Then again maybe I should just work on those song-lyrics a little harder ;)
No, I don’t hope to win a Nobel Prize. If that’s what I’d been after, I certainly would have chosen a different field. Condensed matter physics, say, or quantum things. At least cosmology. But certainly not quantum gravity.
Nobel Prize medal for physics and chemistry. It shows nature in the form of a goddess emerging from the clouds. The veil which covers her face is held up by the Genius of Science. Srsly, see Nobelprize.org. |
But the Nobel Prize is important for science. It’s important not because it singles out a few winners but because in science it’s the one annual event that catches everybody’s attention. On which other day does physics make headlines?
In recent years I heard increasingly louder calls that the Prize-criteria should be amended so that more than three people can win. I am not in favor of that. It doesn’t make sense anyway to hand out exactly one Prize each year regardless of how much progress was made. There is always a long list of people who deserved a Nobel but never got one. Like Vera Rubin, who died last year and who by every reasonable measure should have gotten one. Shame on you, Nobel Committee.
I am particularly opposed to the idea that the Nobel Prize should be awarded to collaborations with members sometimes in the hundreds or even thousands. While the three-people-cutoff is arguably arbitrary, I am not in favor of showering collaboration members with fractional prizes. Things don’t get going because a thousand scientists spontaneously decide to make an experiment. It’s always but a few people who are responsible to make things happen. Those are the ones which the Nobel committee should identify.
So, I am all in favor of the Nobel Prize and like it the way it is. But (leaving aside that many institutions seem to believe Nobel Prize winners lay golden eggs) the Prize has little relevance in research. I definitely know a few people who hope to win it and some even deserve it. But I yet have to meet anyone who deliberately chose their research with that goal in mind.
The Nobel Prize is by construction meant to honor living scientists. This makes sense because otherwise we’d have a backlog of thousands of deceased scientific luminaries and nobody would be interested watching the announcement. But in some research areas we don’t expect to see payoffs in our lifetime. Quantum gravity is one of them.
Personally, I feel less inspired by Nobel Prize winners than by long-dead geniuses like Da Vinci, Leibnitz, or Goethe – masterminds whose intellectual curiosity spanned disciplines. They were ahead of their time and produced writings that not rarely were vague, hard to follow, and sometimes outright wrong. None of them would have won a Nobel Prize had the Prize existed at the time. But their insights laid the basis for centuries of scientific progress.
And so, while we honor those who succeed in the present, let’s not forget that somewhere among us, unrecognized, are the seeds that will grow to next centuries’ discoveries.
Today, as the 2017 Nobel prize is awarded, I want to remind those of you who work in obscure research areas, produce unpopular artworks, or face ridicule for untimely writing, that history will be your final judge, not your contemporaries.
Then again maybe I should just work on those song-lyrics a little harder ;)
Wednesday, September 27, 2017
Dear Dr B: Why are neutrinos evidence for physics beyond the standard model?
Dear Chris,
The standard model of particle physics contains two different types of particles. There are the fermions, which make up matter, and the gauge-bosons which mediate interactions between the fermions and, in some cases, among themselves. There is one additional particle – the Higgs-boson – which is needed to give masses to both bosons and fermions.
The fermions come in left-handed and right-handed versions which are mirror-images of each other. In what I think is the most perplexing feature of the standard model, the left-handed and right-handed versions of fermions behave differently. We say the fermions are “chiral.” The difference between the left- and right-handed particles is most apparent if you look at neutrinos: Nobody has ever seen a right-handed neutrino.
You could say, well, no problem, let’s just get rid of the right-handed neutrinos. Who needs those anyway?
But it’s not that easy because we have known for 20 years or so that neutrinos have masses. We know this because we see them mix or “oscillate” into each other, and such an oscillation requires a non-vanishing mass-difference. This means not all the neutrino-masses can be zero.
Neutrino masses are a complication because the usual way to give masses to fermions is to couple the left-handed version with the right-handed version and with the Higgs. So what do you do if you have no right-handed neutrinos and yet neutrinos are massive?
The current status is therefore that either a) there are right-handed neutrinos but we haven’t yet seen them, or b) neutrinos are different from the other fermions and can get masses in a different way. In either case, the standard model is incomplete.
It is partly an issue of terminology though. Some physicists say right-handed neutrinos are part of the standard model. In this case they aren’t “beyond the standard model” but instead their discovery is pending.
I have a personal fascination with neutrinos because I believe they’ll be key to understanding the pattern of particle-masses. This is because the right-handed neutrino is the only particle in the standard model that doesn’t carry gauge-charges (or they are all zero, respectively). It seems to me that this should be the reason for it either being very heavy or not being there at all. But that’s speculation.
In any case, there many neutrino experiments presently under way to closer study neutrino-oscillations and also to look for “neutrinoless double-beta decay.” The relevance of the latter is that such a decay is possible only if neutrinos are different from the other fermions of the standard model, so that no additional particles are needed to create neutrino masses.
So, no, particle physics isn’t dead and over, it’s still full with discoveries waiting to happen!
Thanks for an interesting question.
See also:
The standard model of particle physics contains two different types of particles. There are the fermions, which make up matter, and the gauge-bosons which mediate interactions between the fermions and, in some cases, among themselves. There is one additional particle – the Higgs-boson – which is needed to give masses to both bosons and fermions.
Neutrino event at the IceCube Observatory in Antarctica. Image: IceCube Collaboration |
The fermions come in left-handed and right-handed versions which are mirror-images of each other. In what I think is the most perplexing feature of the standard model, the left-handed and right-handed versions of fermions behave differently. We say the fermions are “chiral.” The difference between the left- and right-handed particles is most apparent if you look at neutrinos: Nobody has ever seen a right-handed neutrino.
You could say, well, no problem, let’s just get rid of the right-handed neutrinos. Who needs those anyway?
But it’s not that easy because we have known for 20 years or so that neutrinos have masses. We know this because we see them mix or “oscillate” into each other, and such an oscillation requires a non-vanishing mass-difference. This means not all the neutrino-masses can be zero.
Neutrino masses are a complication because the usual way to give masses to fermions is to couple the left-handed version with the right-handed version and with the Higgs. So what do you do if you have no right-handed neutrinos and yet neutrinos are massive?
The current status is therefore that either a) there are right-handed neutrinos but we haven’t yet seen them, or b) neutrinos are different from the other fermions and can get masses in a different way. In either case, the standard model is incomplete.
It is partly an issue of terminology though. Some physicists say right-handed neutrinos are part of the standard model. In this case they aren’t “beyond the standard model” but instead their discovery is pending.
I have a personal fascination with neutrinos because I believe they’ll be key to understanding the pattern of particle-masses. This is because the right-handed neutrino is the only particle in the standard model that doesn’t carry gauge-charges (or they are all zero, respectively). It seems to me that this should be the reason for it either being very heavy or not being there at all. But that’s speculation.
In any case, there many neutrino experiments presently under way to closer study neutrino-oscillations and also to look for “neutrinoless double-beta decay.” The relevance of the latter is that such a decay is possible only if neutrinos are different from the other fermions of the standard model, so that no additional particles are needed to create neutrino masses.
So, no, particle physics isn’t dead and over, it’s still full with discoveries waiting to happen!
Thanks for an interesting question.
See also:
- What are the chances of the universe ending out of nowhere due to vacuum decay?
- Why do physicists worry so much about the black hole information paradox?
- What is emergent gravity?
- Where does dark energy come from and what’s it made of?
- What do physicists mean by “quantum gravity”?
- How come we never hear of a force that the Higgs boson carries?
- Why is Lorentz-invariance in conflict with discreteness?
Thursday, September 21, 2017
The Quantum Quartet
I made some drawings recently. For no particular purpose, really, other than to distract myself.
And here is the joker:
Tuesday, September 19, 2017
Interna
I’m still writing on the book. After not much happened for almost a year, my publisher now rather suddenly asked for the final version of the manuscript. Until that’s done not much will be happening on this blog.
We do seem to have settled on a title though: “Lost in Math: How Beauty Leads Physics Astray.” The title is my doing, the subtitle isn’t. I just hope it won’t lead too many readers astray.
The book is supposed to be published in the USA/Canada by Basic Books next year in the Spring, and in Germany by Fischer half a year later. I’ll tell you more about the content at some point but right now I’m pretty sick of the whole book-thing.
In the meantime I have edited another book, this one on “Experimental Search for Quantum Gravity” which you can now preoder on amazon. It’s a, probably rather hard to digest, collection of essays about topics covered at a conference I organized last year. I merely wrote the preface.
Yesterday the twins had their first day in school. As is unfortunately still common in Germany, classes go only until noon. And so, we’re now trying a new arrangement to keep the kids occupied throughout the working day.
We do seem to have settled on a title though: “Lost in Math: How Beauty Leads Physics Astray.” The title is my doing, the subtitle isn’t. I just hope it won’t lead too many readers astray.
The book is supposed to be published in the USA/Canada by Basic Books next year in the Spring, and in Germany by Fischer half a year later. I’ll tell you more about the content at some point but right now I’m pretty sick of the whole book-thing.
In the meantime I have edited another book, this one on “Experimental Search for Quantum Gravity” which you can now preoder on amazon. It’s a, probably rather hard to digest, collection of essays about topics covered at a conference I organized last year. I merely wrote the preface.
Yesterday the twins had their first day in school. As is unfortunately still common in Germany, classes go only until noon. And so, we’re now trying a new arrangement to keep the kids occupied throughout the working day.
Wednesday, September 13, 2017
Away Note
I'm in Switzerland this week, for a conference on "Thinking about Space and Time: 100 Years of Applying and Interpreting General Relativity." I am also behind with several things and blogging will remain slow for the next weeks. If you miss my writing all too much, here is a new paper.
Wednesday, September 06, 2017
Wednesday, August 30, 2017
The annotated math of (almost) everything
Have you heard of the principle of least action? It’s the most important idea in physics, and it underlies everything. According to this principle, our reality is optimal in a mathematically exact way: it minimizes a function called the “action.” The universe that we find ourselves in is the one for which the action takes on the smallest value.
In quantum mechanics, reality isn’t quite that optimal. Quantum fields don’t have to decide on one specific configuration; they can do everything they want, and the action then quantifies the weight of each contribution. The sum of all these contributions – known as the path-integral – describes again what we observe.
This omniscient action has very little to do with “action” as in “action hero”. It’s simply an integral, usually denoted S, over another function, called the Lagrangian, usually denoted L. There’s a Lagrangian for the Standard Model and one for General Relativity. Taken together they encode the behavior of everything that we know of, except dark matter and quantum gravity.
With a little practice, there’s a lot you can read off directly from the Lagrangian, about the behavior of the theory at low or high energies, about the type of fields and mediator fields, and about the type of interaction.
The below figure gives you a rough idea how that works.
I originally made this figure for the appendix of my book, but later removed it. Yes, my editor is still optimistic the book will be published Spring 2018. The decision about this will fall in the next month or so, so stay tuned.
In quantum mechanics, reality isn’t quite that optimal. Quantum fields don’t have to decide on one specific configuration; they can do everything they want, and the action then quantifies the weight of each contribution. The sum of all these contributions – known as the path-integral – describes again what we observe.
This omniscient action has very little to do with “action” as in “action hero”. It’s simply an integral, usually denoted S, over another function, called the Lagrangian, usually denoted L. There’s a Lagrangian for the Standard Model and one for General Relativity. Taken together they encode the behavior of everything that we know of, except dark matter and quantum gravity.
With a little practice, there’s a lot you can read off directly from the Lagrangian, about the behavior of the theory at low or high energies, about the type of fields and mediator fields, and about the type of interaction.
The below figure gives you a rough idea how that works.
I originally made this figure for the appendix of my book, but later removed it. Yes, my editor is still optimistic the book will be published Spring 2018. The decision about this will fall in the next month or so, so stay tuned.
Wednesday, August 23, 2017
I was wrong. You were wrong too. Admit it.
I thought that anti-vaxxers are a US-phenomenon, certainly not to be found among the dutiful Germans. Well, I was wrong. The WHO estimates only 93% of children in Germany receive both measles shots.
I thought that genes determine sex. I was wrong. For certain species of fish and reptiles that’s not the case.
I thought that ultrasound may be a promising way to wirelessly transfer energy. That was wrong too.
Don’t worry, I haven’t suddenly developed a masochist edge. I’ve had an argument. Not my every-day argument about dark matter versus modified gravity and similar academic problems. This one was about Donald Trump and how to be wrong the right way.
Trump changes his mind. A lot. May that be about the NATO or about Afghanistan or, really, find me anything he has not changed his mind about.
Now, I suspect that’s because he doesn’t have an opinion, can’t recall what he said last time, and just hopes no one notices he wings that presidency thing. But whatever the reason, Trump’s mental flexibility is a virtue to strive for. You can see how that didn’t sit well with my liberal friends.
It’s usually hard to change someone’s mind, and a depressingly large amount of studies have shown that evidence isn’t enough to do it. Presenting people with evidence contradicting their convictions can even have the very opposite effect of reinforcing their opinions.
We hold on to our opinions, strongly. Constructing consistent explanations for the world is hard work, and we don’t like others picking apart the stories we settled on. The quirks of the human mind can be tricky – tricky to understand and tricky to overcome. Psychology is part of it. But my recent argument over Trump’s wrongness made me think about the part sociology has in our willingness to change opinion. It’s bad enough to admit to yourself you were wrong. It’s far worse to admit to other people you were wrong.
You see this play out in almost every comment section on social media. People defend hopeless positions, go through rhetorical tricks and textbook fallacies, appeal to authority, build straw men, and slide red herrings down slippery slopes. At the end, there’s always good, old denial. Anything, really, to avoid saying “I was wrong.”
And the more public an opinion was stated, the harder it becomes to backpedal. The more you have chosen friends by their like-mindedness, and the more they count on your like-mindedness, the higher the stakes for being unlike. The more widely known you are, the harder it is to tell your followers you won’t deliver arguments for them any longer. Turn your back on them. Disappoint them. Lose them.
It adds to this that public conversations encourage us to make up opinions on the fly. The three examples I listed above had one thing in common. In neither case did I actually know much about what I was saying. It wasn’t that I had wrong information – I simply had no information, and it didn’t occur to me to check, or maybe I just wasn’t interested enough. I was just hoping nobody would notice. I was winging it. You wouldn’t want me as president either.
But enough of the public self-flagellation and back to my usual self. Science is about being wrong more than it is about being right. By the time you have a PhD you’ll have been wrong in countless ways, so many ways indeed it’s not uncommon students despair over their seeming incapability until reassured we’ve all been there.
Science taught me it’s possible to be wrong gracefully, and – as with everything in life – it becomes easier with practice. And it becomes easier if you see other people giving examples. So what have you recently changed your mind about?
I thought that genes determine sex. I was wrong. For certain species of fish and reptiles that’s not the case.
I thought that ultrasound may be a promising way to wirelessly transfer energy. That was wrong too.
Don’t worry, I haven’t suddenly developed a masochist edge. I’ve had an argument. Not my every-day argument about dark matter versus modified gravity and similar academic problems. This one was about Donald Trump and how to be wrong the right way.
Percentage of infants receiving 2nd dose of measles vaccine in Germany. [Source: WHO] |
Trump changes his mind. A lot. May that be about the NATO or about Afghanistan or, really, find me anything he has not changed his mind about.
Now, I suspect that’s because he doesn’t have an opinion, can’t recall what he said last time, and just hopes no one notices he wings that presidency thing. But whatever the reason, Trump’s mental flexibility is a virtue to strive for. You can see how that didn’t sit well with my liberal friends.
It’s usually hard to change someone’s mind, and a depressingly large amount of studies have shown that evidence isn’t enough to do it. Presenting people with evidence contradicting their convictions can even have the very opposite effect of reinforcing their opinions.
We hold on to our opinions, strongly. Constructing consistent explanations for the world is hard work, and we don’t like others picking apart the stories we settled on. The quirks of the human mind can be tricky – tricky to understand and tricky to overcome. Psychology is part of it. But my recent argument over Trump’s wrongness made me think about the part sociology has in our willingness to change opinion. It’s bad enough to admit to yourself you were wrong. It’s far worse to admit to other people you were wrong.
You see this play out in almost every comment section on social media. People defend hopeless positions, go through rhetorical tricks and textbook fallacies, appeal to authority, build straw men, and slide red herrings down slippery slopes. At the end, there’s always good, old denial. Anything, really, to avoid saying “I was wrong.”
And the more public an opinion was stated, the harder it becomes to backpedal. The more you have chosen friends by their like-mindedness, and the more they count on your like-mindedness, the higher the stakes for being unlike. The more widely known you are, the harder it is to tell your followers you won’t deliver arguments for them any longer. Turn your back on them. Disappoint them. Lose them.
It adds to this that public conversations encourage us to make up opinions on the fly. The three examples I listed above had one thing in common. In neither case did I actually know much about what I was saying. It wasn’t that I had wrong information – I simply had no information, and it didn’t occur to me to check, or maybe I just wasn’t interested enough. I was just hoping nobody would notice. I was winging it. You wouldn’t want me as president either.
But enough of the public self-flagellation and back to my usual self. Science is about being wrong more than it is about being right. By the time you have a PhD you’ll have been wrong in countless ways, so many ways indeed it’s not uncommon students despair over their seeming incapability until reassured we’ve all been there.
Science taught me it’s possible to be wrong gracefully, and – as with everything in life – it becomes easier with practice. And it becomes easier if you see other people giving examples. So what have you recently changed your mind about?
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