Define “better”

Dark matter remains undetected in the laboratory. This has been true for forever, so I don’t know what drives the timing of the recent spate of articles encouraging us to keep the faith, that dark matter is still a better idea than anything else. This depends on how we define “better.”

There is a long-standing debate in the philosophy of science about the relative merits of accommodation and prediction. A scientific theory should have predictive power. It should also explain all the relevant data. To do the latter almost inevitably requires some flexibility in order to accommodate things that didn’t turn out exactly as predicted. What is the right mix? Do we lean more towards prediction, or accommodation? The answer to that defines “better” in this context.

One of the recent articles is titled “The dark matter hypothesis isn’t perfect, but the alternatives are worse” by Paul Sutter. This perfectly encapsulates the choice one has to make in what is unavoidably a value judgement. Is it better to accommodate, or to predict (see the Spergel Principle)? Dr. Sutter comes down on the side of accommodation. He notes a couple of failed predictions of dark matter, but mentions no specific predictions of MOND (successful or not) while concluding that dark matter is better because it explains more.

One important principle in science is objectivity. We should be even-handed in the evaluation of evidence for and against a theory. In practice, that is very difficult. As I’ve written before, it made me angry when the predictions of MOND came true in my data for low surface brightness galaxies. I wanted dark matter to be right. I felt sure that it had to be. So why did this stupid MOND theory have any of its predictions come true?

One way to check your objectivity is to look at it from both sides. If I put on a dark matter hat, then I largely agree with what Dr. Sutter says. To quote one example:

The dark matter hypothesis isn’t perfect. But then again, no scientific hypothesis is. When evaluating competing hypotheses, scientists can’t just go with their guts, or pick one that sounds cooler or seems simpler. We have to follow the evidence, wherever it leads. In almost 50 years, nobody has come up with a MOND-like theory that can explain the wealth of data we have about the universe. That doesn’t make MOND wrong, but it does make it a far weaker alternative to dark matter.
Paul Sutter

OK, so now let’s put on a MOND hat. Can I make the same statement?

The MOND hypothesis isn’t perfect. But then again, no scientific hypothesis is. When evaluating competing hypotheses, scientists can’t just go with their guts, or pick one that sounds cooler or seems simpler. We have to follow the evidence, wherever it leads. In almost 50 years, nobody has detected dark matter, nor come up with a dark matter-based theory with the predictive power of MOND. That doesn’t make dark matter wrong, but it does make it a far weaker alternative to MOND.

So, which of these statements is true? Well, both of them. How do we weigh the various lines of evidence? Is it more important to explain a large variety of the data, or to be able to predict some of it? This is one of the great challenges when comparing dark matter and MOND. They are incommensurate: the set of relevant data is not the same for both. MOND makes no pretense to provide a theory of cosmology, so it doesn’t even attempt to explain much of the data so beloved by cosmologists. Dark matter explains everything, but, broadly defined, it is not a theory so much as an inference – assuming gravitational dynamics are inviolate, we need more mass than meets the eye. It’s a classic case of comparing apples and oranges.

While dark matter is a vague concept in general, one can build specific theories of dark matter that are predictive. Simulations with generic cold dark matter particles predict cuspy dark matter halos. Galaxies are thought to reside in these halos, which dominate their dynamics. This overlaps with the predictions of MOND, which follow from the observed distribution of normal matter. So, do galaxies look like tracer particles orbiting in cuspy halos? Or do their dynamics follow from the observed distribution of light via Milgrom’s strange formula? The relevant subset of the data very clearly indicate the latter. When head-to-head comparisons like this can be made, the a priori predictions of MOND win, hands down, over and over again. [If this statement sounds wrong, try reading the relevant scientific literature. Being an expert on dark matter does not automatically make one an expert on MOND. To be qualified to comment, one should know what predictive successes MOND has had. People who say variations of “MOND only fits rotation curves” are proudly proclaiming that they lack this knowledge.]

It boils down to this: if you want to explain extragalactic phenomena, use dark matter. If you want to make a prediction – in advance! – that will come true, use MOND.

A lot of the debate comes down to claims that anything MOND can do, dark matter can do better. Or at least as well. Or, if not as well, good enough. This is why conventionalists are always harping about feedback: it is the deus ex machina they invoke in any situation where they need to explain why their prediction failed. This does nothing to explain why MOND succeeded where they failed.

This post-hoc reasoning is profoundly unsatisfactory. Dark matter, being invisible, allows us lots of freedom to cook up an explanation for pretty much anything. My long-standing concern for the dark matter paradigm is not the failure of any particular prediction, but that, like epicycles, it has too much explanatory power. We could use it to explain pretty much anything. Rotation curves flat when they should be falling? Add some dark matter. No such need? No dark matter. Rising rotation curves? Sure, we could explain that too: add more dark matter. Only we don’t, because that situation doesn’t arise in nature. But we could if we had to. (See, e.g., Fig. 6 of de Blok & McGaugh 1998.)

There is no requirement in dark matter that rotation curves be as flat as they are. If we start from the prior knowledge that they are, then of course that’s what we get. If instead we independently try to build models of galactic disks in dark matter halos, very few of them wind up with realistic looking rotation curves. This shouldn’t be surprising: there are, in principle, an uncountably infinite number of combinations of galaxies and dark matter halos. Even if we impose some sensible restrictions (e.g., scaling the mass of one component with that of the other), we still don’t get it right. That’s one reason that we have to add feedback, which suffices according to some, and not according to others.

In contrast, the predictions of MOND are unique. The kinematics of an object follow from its observed mass distribution. The two are tied together by the hypothesized force law. There is a one-to-one relation between what you see and what you get.

This was not expected in dark matter. It makes no sense that this should be so. The baryonic tail should not wag the dark matter dog.

From the perspective of building dark matter models, it’s like the proverbial needle in the haystack: the haystack is the volume of possible baryonic disk plus dark matter halo combinations; the one that “looks like” MOND is the needle. Somehow nature plucks the MOND-like needle out of the dark matter haystack every time it makes a galaxy.

The dark matter haystack. Galaxies might lie anywhere in this voluminous, multiparameter space, but in practice they inevitably seem to reside in the negligibly small part of the volume that “looks like” MOND.

Dr. Sutter says that we shouldn’t go with our gut. That’s exactly what I wanted to do, long ago, to maintain my preference for dark matter. I’d love to do that now so that I could stop having this argument with otherwise reasonable people.

Instead of going with my gut, I’m making a probabilistic statement. In Bayesian terms, the odds of observing MONDian behavior given the prior that we live in a universe made of dark matter are practically zero. In MOND, observing MONDian behavior is the only thing that can happen. That’s what we observe in galaxies, over and over again. Any information criterion shows a strong quantitative preference for MOND when dynamical evidence is considered. That does not happen when cosmological data are considered because MOND makes no prediction there. Concluding that dark matter is better overlooks the practical impossibility that MOND-like phenomenolgy is observed at all. Of course, once one knows this is what the data show, it seems a lot more likely, and I can see that effect in the literature over the long arc of scientific history. This is why, to me, predictive power is more important than accommodation: what we predict before we know the answer is more important than whatever we make up once the answer is known.

The successes of MOND are sometimes minimized by lumping all galaxies into a single category. That’s not correct. Every galaxy has a unique mass distribution; each one is an independent test. The data for galaxies extend over a large dynamic range, from dwarfs to giants, from low to high surface brightness, from gas to star dominated cases. Dismissing this by saying “MOND only explains rotation curves” is like dismissing Newton for only explaining planets – as if every planet, moon, comet, and asteroid aren’t independent tests of Newton’s inverse square law.

Two galaxies with very different mass distributions. Neither are well explained by dark matter, which provides no reason for the detailed shapes encapsulated by Sancisi’s Law. In contrast, MOND describes these naturally: features in the rotation curves follow from those in the baryon distributions because the force law tells them to.

MOND does explain more that rotation curves. That was the first thing I checked. I spent several years looking at all of the data, and have reviewed the situation many times since. What I found surprising is how much MOND explains, if you let it. More disturbing was how often I came across claims in the literature that MOND was falsified by X only to try the analysis myself and find that, no, if you bother to do it right, that’s pretty much just what it predicts. Not in every case, of course – no hypothesis is perfect – but I stopped bothering after several hundred cases. Literally hundreds. I can’t keep up with every new claim, and it isn’t my job to do so. My experience has been that as the data improve, so too does its agreement with MOND.

Dr. Sutter’s article goes farther, repeating a common misconception that “the tweaking of gravity under MOND is explicitly designed to explain the motions of stars within galaxies.” This is an overstatement so strong as to be factually wrong. MOND was explicitly designed to produce flat rotation curves – as was dark matter. However, there is a lot more to it than that. Once we write down the force law, we’re stuck with it. It has lots of other unavoidable consequences that lead to genuine predictions. Milgrom explicitly laid out what these consequences would be, and basically all of them have subsequently been observed. I include a partial table in my last review; it only ends where it does because I had to stop somewhere. These were genuine, successful, a priori predictions – the gold standard in science. Some of them can be explained with dark matter, but many cannot: they make no sense, and dark matter can only accommodate them thanks to its epic flexibility.

Dr. Sutter makes a number of other interesting points. He says we shouldn’t “pick [a hypothesis] that sounds cooler or seems simpler.” I’m not sure which seems cooler here – a universe pervaded by a mysterious invisible mass that we can’t [yet] detect in the laboratory but nevertheless controls most of what goes on out there seems pretty cool to me. That there might also be some fundamental aspect of the basic theory of gravitational dynamics that we’re missing also seems like a pretty cool possibility. Those are purely value judgments.

Simplicity, however, is a scientific value known as Occam’s razor. The simpler of competing theories is to be preferred. That’s clearly MOND: we make one adjustment to the force law, and that’s it. What we lack is a widely accepted, more general theory that encapsulates both MOND and General Relativity.

In dark matter, we multiply entities unnecessarily – there is extra mass composed of unknown particles that have no place in the Standard Model of particle physics (which is quite full up) so we have to imagine physics beyond the standard model and perhaps an entire dark sector because why just one particle when 85% of the mass is dark? and there could also be dark photons to exchange forces that are only active in the dark sector as well as entire hierarchies of dark particles that maybe have their own ecosystem of dark stars, dark planets, and maybe even dark people. We, being part of the “normal” matter, are just a minority constituent of this dark universe; a negligible bit of flotsam compared to the dark sector. Doesn’t it make sense to imagine that the dark sector has as rich and diverse a set of phenomena as the “normal” sector? Sure – if you don’t mind abandoning Occam’s razor. Note that I didn’t make any of this stuff up; everything I said in that breathless run-on sentence I’ve heard said by earnest scientists enthusiastic about how cool the dark sector could be. Bugger Occam.

There is also the matter of timescales. Dr. Sutter mentions that “In almost 50 years, nobody has come up with a MOND-like theory” that does all that we need it to do. That’s true, but for the typo. Next year (2023) will mark the 40th anniversary of Milgrom’s first publications on MOND, so it hasn’t been half a century yet. But I’ve heard recurring complaints to this effect before, that finding the deeper theory is taking too long. Let’s examine that, shall we?

First, remember some history. When Newton introduced his inverse square law of universal gravity, it was promptly criticized as a form of magical thinking: How, Sir, can you have action at a distance? The conception at the time was that you had to be in physical contact with an object to exert a force on it. For the sun to exert a force on the earth, or the earth on the moon, seemed outright magical. Leibnitz famously accused Newton of introducing ‘occult’ forces. As a consequence, Newton was careful to preface his description of universal gravity as everything happening as if the force was his famous inverse square law. The “as if” is doing a lot of work here, basically saying, in modern parlance “OK, I don’t get how this is possible, I know it seems really weird, but that’s what it looks like.” I say the same about MOND: galaxies behave as if MOND is the effective force law. The question is why.

As near as I can tell from reading the history around this, and I don’t know how clear this is, but it looks like it took about 20 years for Newton to realize that there was a good geometric reason for the inverse square law. We expect our freshman physics students to see that immediately. Obviously Newton was smarter than the average freshman, so why’d it take so long? Was he, perhaps, preoccupied with the legitimate-seeming criticisms of action at a distance? It is hard to see past a fundamental stumbling block like that, and I wonder if the situation now is analogous. Perhaps we are missing something now that will seems obvious in retrospect, distracted by criticisms that will seem absurd in the future.

Many famous scientists built on the dynamics introduced by Newton. The Poisson equation isn’t named the Newton equation because Newton didn’t come up with it even though it is fundamental to Newtonian dynamics. Same for the Lagrangian. And the classical Hamiltonian. These developments came many decades after Newton himself, and required the efforts of many brilliant scientists integrated over a lot of time. By that standard, forty years seems pretty short: one doesn’t arrive at a theory of everything overnight.

What is the right measure? The integrated effort of the scientific community is more relevant than absolute time. Over the past forty years, I’ve seen a lot of push back against even considering MOND as a legitimate theory. Don’t talk about that! This isn’t exactly encouraging, so not many people have worked on it. I can count on my fingers the number of people who have made important contributions to the theoretical development of MOND. (I am not one of them. I am an observer following the evidence, wherever it leads, even against my gut feeling and to the manifest detriment of my career.) It is hard to make progress without a critical mass of people working on a problem.

Of course, people have been looking for dark matter for those same 40 years. More, really – if you want to go back to Oort and Zwicky, it has been 90 years. But for the first half century of dark matter, no one was looking hard for it – it took that long to gel as a serious problem. These things take time.

Nevertheless, for several decades now there has been an enormous amount of effort put into all aspects of the search for dark matter: experimental, observational, and theoretical. There is and has been a critical mass of people working on it for a long time. There have been thousands of talented scientists who have contributed to direct detection experiments in dozens of vast underground laboratories, who have combed through data from X-ray and gamma-ray observatories looking for the telltale signs of dark matter decay or annihilation, who have checked for the direct production of dark matter particles in the LHC; even theorists who continue to hypothesize what the heck the dark matter could be and how we might go about detecting it. This research has been well funded, with billions of dollars having been spent in the quest for dark matter. And what do we have to show for it?

Zero. Nada. Zilch. Squat. A whole lot of nothing.

This is equal to the amount of funding that goes to support research on MOND. There is no faster way to get a grant proposal rejected than to say nice things about MOND. So one the one hand, we have a small number of people working on the proverbial shoestring, while on the other, we have a huge community that has poured vast resources into the attempt to detect dark matter. If we really believe it is taking too long, perhaps we should try funding MOND as generously as we do dark matter.

By the wayside

I noted last time that in the rush to analyze the first of the JWST data, that “some of these candidate high redshift galaxies will fall by the wayside.” As Maurice Aabe notes in the comments there, this has already happened.

I was concerned because of previous work with Jay Franck in which we found that photometric redshifts were simply not adequately precise to identify the clusters and protoclusters we were looking for. Consequently, we made it a selection criterion when constructing the CCPC to require spectroscopic redshifts. The issue then was that it wasn’t good enough to have a rough idea of the redshift, as the photometric method often provides (what exactly it provides depends in a complicated way on the redshift range, the stellar population modeling, and the wavelength range covered by the observational data that is available). To identify a candidate protocluster, you want to know that all the potential member galaxies are really at the same redshift.

This requirement is somewhat relaxed for the field population, in which a common approach is to ask broader questions of the data like “how many galaxies are at z ~ 6? z ~ 7?” etc. Photometric redshifts, when done properly, ought to suffice for this. However, I had noticed in Jay’s work that there were times when apparently reasonable photometric redshift estimates went badly wrong. So it made the ganglia twitch when I noticed that in early JWST work – specifically Table 2 of the first version of a paper by Adams et al. – there were seven objects with candidate photometric redshifts, and three already had a preexisting spectroscopic redshift. The photometric redshifts were mostly around z ~ 9.7, but the three spectroscopic redshifts were all smaller: two z ~ 7.6, one 8.5.

Three objects are not enough to infer a systematic bias, so I made a mental note and moved on. But given our previous experience, it did not inspire confidence that all the available cases disagreed, and that all the spectroscopic redshifts were lower than the photometric estimates. These things combined to give this observer a serious case of “the heebie-jeebies.”

Adams et al have now posted a revised analysis in which many (not all) redshifts change, and change by a lot. Here is their new Table 4:

*Table 4 from Adams et al. (2022, version 2).*

There are some cases here that appear to confirm and improve the initial estimate of a high redshift. For example, SMACS-z11e had a very uncertain initial redshift estimate. In the revised analysis, it is still at z~11, but with much higher confidence.

That said, it is hard to put a positive spin on these numbers. 23 of 31 redshifts change, and many change drastically. Those that change all become smaller. The highest surviving redshift estimate is z ~ 15 for SMACS-z16b. Among the objects with very high candidate redshifts, some are practically local (e.g., SMACS-z12a, F150DB-075, F150DA-058).

So… I had expected that this could go wrong, but I didn’t think it would go this wrong. I was concerned about the photometric redshift method – how well we can model stellar populations, especially at young ages dominated by short lived stars that in the early universe are presumably lower metallicity than well-studied nearby examples, the degeneracies between galaxies at very different redshifts but presenting similar colors over a finite range of observed passbands, dust (the eternal scourge of observational astronomy, expected to be an especially severe affliction in the ultraviolet that gets redshifted into the near-IR for high-z objects, both because dust is very efficient at scattering UV photons and because this efficiency varies a lot with metallicity and the exact gran size distribution of the dust), when is a dropout really a dropout indicating the location of the Lyman break and when is it just a lousy upper limit of a shabby detection, etc. – I could go on, but I think I already have. It will take time to sort these things out, even in the best of worlds.

We do not live in the best of worlds.

It appears that a big part of the current uncertainty is a calibration error. There is a pipeline for handling JWST data that has an in-built calibration for how many counts in a JWST image correspond to what astronomical magnitude. The JWST instrument team warned us that the initial estimate of this calibration would “improve as we go deeper into Cycle 1” – see slide 13 of Jane Rigby’s AAS presentation.

I was not previously aware of this caveat, though I’m certainly not surprised by it. This is how these things work – one makes an initial estimate based on the available data, and one improves it as more data become available. Apparently, JWST is outperforming its specs, so it is seeing as much as 0.3 magnitudes deeper than anticipated. This means that people were inferring objects to be that much too bright, hence the appearance of lots of galaxies that seem to be brighter than expected, and an apparent systematic bias to high z for photometric redshift estimators.

I was not at the AAS meeting, let alone Dr. Rigby’s presentation there. Even if I had been, I’m not sure I would have appreciated the potential impact of that last bullet point on nearly the last slide. So I’m not the least bit surprised that this error has propagated into the literature. This is unfortunate, but at least this time it didn’t lead to something as bad as the Challenger space shuttle disaster in which the relevant warning from the engineers was reputed to have been buried in an obscure bullet point list.

So now we need to take a deep breath and do things right. I understand the urgency to get the first exciting results out, and they are still exciting. There are still some interesting high z candidate galaxies, and lots of empirical evidence predating JWST indicating that galaxies may have become too big too soon. However, we can only begin to argue about the interpretation of this once we agree to what the facts are. At this juncture, it is more important to get the numbers right than to post early, potentially ill-advised takes on arXiv.

That said, I’d like to go back to writing my own ill-advised take to post on arXiv now.

LZ: another non-detection

Just as I was leaving for a week’s vacation, the dark matter search experiment LZ reported its first results. Now that I’m back, I see that I didn’t miss anything. Here is their figure of merit:

The latest experimental limits on WIMP dark matter from LZ (arXiv:2207.03764). The parameter space above the line is excluded. Note the scale on the y-axis bearing in mind that the original expectation was for a cross section around 10^-39 cm², well above the top edge of this graph.

LZ is a merger of two previous experiments compelled to grow still bigger in the never-ending search for dark matter. It contains “seven active tonnes of liquid xenon,” which is an absurd amount, being a substantial fraction of the entire terrestrial supply. It all has to be super-cooled to near absolute zero and filtered of all contaminants that might include naturally radioactive isotopes that might mimic the sought-after signal of dark matter scattering off of xenon nuclei. It is a technological tour de force.

The technology is really fantastic. The experimentalists have accomplished amazing things in building these detectors. They have accomplished the target sensitivity, and then some. If WIMPs existed, they should have found them by now.

WIMPs have not been discovered. As the experiments have improved, the theorists have been obliged to repeatedly move the goalposts. The original (1980s) expectation for the interaction cross-section was 10^-39 cm². That was quickly excluded, but more careful (1990s) calculation suggested perhaps more like 10^-42 cm². This was also excluded experimentally. By the late 2000s, the “prediction” had migrated to 10^-46 cm². This has also now been excluded, so the goalposts have been moved to 10^-48 cm². This migration has been driven entirely by the data; there is nothing miraculous about a WIMP with this cross section.

As remarkable a technological accomplishment as experiments like LZ are, they are becoming the definition of insanity: repeating the same action but expecting a different result.

For comparison, consider the LIGO detection of gravitational waves. A large team of scientists worked unspeakably hard to achieve the detection of a tiny effect. It took 40 years of failure before success was obtained. Until that point, it seemed much the same: repeating the same action but expecting a different result.

Except it wasn’t, because there was a clear expectation for the sensitivity that was required to detect gravitational waves. Once that sensitivity was achieved, they were detected. It wasn’t that simple of course, but close enough for our purposes: it took a long time to get where they were going, but they achieved success once they got there. Having a clear prediction is essential.

In the case of WIMP searches, there was also a clear prediction. The required sensitivity was achieved – long ago. Nothing was found, so the goalposts were moved – by a lot. Then the new required sensitivity was achieved, still without detection. Repeatedly.

It always makes sense to look harder for something you expect if at first you don’t succeed. But at some point, you have to give up: you ain’t gonna find it. This is disappointing, but we’ve all experienced this kind of disappointment at some point in our lives. The tricky part is deciding when to give up.

In science, the point to give up is when your hypothesis is falsified. The original WIMP hypothesis was falsified a long time ago. We keep it on life support with modifications, often obfuscating (to our students and to ourselves) that the WIMPs we’re talking about today are no longer the WIMPs we originally conceived.

I sometimes like to imagine the thought experiment of sending some of the more zealous WIMP advocates back in time to talk to their younger selves. What would they say? How would they respond to themselves? These are not people who like to be contradicted by anyone, even themselves, so I suspect it would go something like

Old scientist: “Hey, kid – I’m future you. This experiment you’re about to spend your life working on won’t detect what you’re looking for.”
Young scientist: “Uh huh. You say you’re me from the future, Mr. Credibility? Tell me: at what point do I go senile, you doddering old fool?”
Old scientist: “You don’t. It just won’t work out the way you think. On top of dark matter, there’s also dark energy…”
Young scientist: “What the heck is dark energy, you drooling crackpot?”
Old scientist: “The cosmological constant.”
Young scientist: “The cosmological constant! You can’t expect people to take you seriously talking about that rubbish. GTFO.”

That’s the polite version that doesn’t end in fisticuffs. It’s easy to imagine this conversation going south much faster. I know that if 1993 me had received a visit from 1998 me telling me that in five years I would have come to doubt WIMPs, and also would have demonstrated that the answer to the missing mass problem might not be dark matter at all, I… would not have taken it well.

That’s why predictions are important in science. They tell us when to change our mind. When to stop what we’re doing because it’s not working. When to admit that we were wrong, and maybe consider something else. Maybe that something else won’t prove correct. Maybe the next ten something elses won’t. But we’ll never find out if we won’t let go of the first wrong thing.

Some Outsider Perspective from Insiders

Avi Loeb has a nice recent post Recalculating Academia, in which he discusses some of the issues confronting modern academia. One of the reasons I haven’t written here for a couple of months is despondency over the same problems. If you’re here reading this, you’ll likely be interested in what he has to say.

I am not eager to write at length today, but I do want to amplify some of the examples he gives with my own experience. For example, he notes that there are

theoretical physicists who avoid the guillotine of empirical tests for half a century by dedicating their career to abstract conjectures, avoid the risk of being proven wrong while demonstrating mathematical virtuosity.
Avi Loeb

I recognize many kinds of theoretical physicists who fit this description. My first thought was string theory, which took off in the mid-80s when I was a grad student at Princeton, ground zero for that movement in the US. (The Russians indulged in this independently.) I remember a colloquium in which David Gross advocated the “theory of everything” with gratuitous religious fervor to a large audience of eager listeners quavering with anticipation with the texture of religious revelation. It was captivating and convincing, up until the point near the end when he noted that experimental tests were many orders of magnitude beyond any experiment conceivable at the time. That… wasn’t physics to me. If this was the path the field was going down, I wanted no part of it. This was one of many factors that precipitated my departure from the toxic sludge that was grad student life in the Princeton physics department.

I wish I could say I had been proven wrong. Instead, decades later, physics has nothing to show for its embrace of string theory. There have been some impressive development in mathematics stemming from it. Mathematics, not physics. And yet, there persists a large community of theoretical physicists who wander endlessly in the barren and practically infinite parameter space of multidimensional string theory. Maybe there is something relevant to physical reality there, or maybe it hasn’t been found because there isn’t. At what point does one admit that the objective being sought just ain’t there? [Death. For many people, the answer seems to be never. They keep repeating the same fruitless endeavor until they die.]

We do have new physics, in the form of massive neutrinos and the dark matter problem and the apparent acceleration of the expansion rate of the universe. What we don’t have is the expected evidence for supersymmetry, the crazy-bold yet comparatively humble first step on the road to string theory. If they had got even this much right, we should have seen evidence for it at the LHC, for example in the decay of the aptly named B_S meson. If supersymmetric particles existed, they should provide many options for the meson to decay into, which otherwise has few options in the Standard Model of particle physics. This was a strong prediction of minimal supersymmetry, so much so that it was called the Golden Test of supersymmetry. After hearing this over and over in the ’80s and ’90s, I have not heard it again any time in this century. I’m nor sure when the theorists stopped talking about this embarrassment, but I suspect it is long enough ago now that it will come as a surprise to younger scientists, even those who work in the field. Supersymmetry flunked the golden test, and it flunked it hard. Rather than abandon the theory (some did), we just stopped talking about. There persists a large community of theorists who take supersymmetry for granted, and react with hostility if you question that Obvious Truth. They will tell you with condescension that only minimal supersymmetry is ruled out; there is an enormous parameter space still open for their imaginations to run wild, unbridled by experimental constraint. This is both true and pathetic.

Reading about the history of physics, I learned that there was a community of physicists who persisted believing in aether for decades after the Michelson-Morley experiment. After all, only some forms of aether were ruled out. This was true, at the time, but we don’t bother with that detail when teaching physics now. Instead, it gets streamlined to “aether was falsified by Michelson-Morley.” This is, in retrospect, true, and we don’t bother to mention those who pathetically kept after it.

The standard candidate for dark matter, the WIMP, is a supersymmetric particle. If supersymmetry is wrong, WIMPs don’t exist. And yet, there is a large community of particle physicists who persist in building ever bigger and better experiments designed to detect WIMPs. Funny enough, they haven’t detected anything. It was a good hypothesis, 38 years ago. Now its just a bad habit. The better ones tacitly acknowledge this, attributing their continuing efforts to the streetlight effect: you look where you can see.

Prof. Loeb offers another pertinent example:

When I ask graduating students at their thesis exam whether the cold dark matter paradigm will be proven wrong if their computer simulations will be in conflict with future data, they almost always say that any disagreement will indicate that they should add a missing ingredient to their theoretical model in order to “fix” the discrepancy.
Avi Loeb

This is indeed the attitude. So much so that no additional ingredient seems to absurd if it is what we need to save the phenomenon. Feedback is the obvious example in my own field, as that (or the synonyms “baryon physics” or “gastrophysics”) is invoked to explain away any and all discrepancies. It sounds simple, since feedback is a real effect that does happen, but this single word does a lot of complicated work under the hood. There are many distinct kinds of feedback: stellar winds, UV radiation from massive stars, supernova when those stars explode, X-rays from compact sources like neutron stars, and relativistic jets from supermasive black holes at the centers of galactic nuclei. These are the examples of feedback that I can think of off the top of my head, there are probably more. All of these things have perceptible, real-world effects on the relevant scales, with, for example, stars blowing apart the dust and gas of their stellar cocoons after they form. This very real process has bugger all to do with what feedback is invoked to do on galactic scales. Usually, supernova are blamed by theorists for any and all problems in dwarf galaxies, while observers tell me that stellar winds do most of the work in disrupting star forming regions. Confronted with this apparent discrepancy, the usual answer is that it doesn’t matter how the energy is input into the interstellar medium, just that it is. Yet we can see profound differences between stellar winds and supernova explosions, so this does not inspire confidence for the predictive power of theories that generically invoke feedback to explain away problems that wouldn’t be there in a healthy theory.

This started a long time ago. I had already lost patience with this unscientific attitude to the point that I dubbed it the

Spergel Principle: “It is better to postdict than to predict.”
McGaugh 1998

This continues to go on and has now done so for so long that generations of students seem to think that this is how science is supposed to be done. If asked about hypothesis testing and whether a theory can be falsified, many theorists will first look mystified, then act put out. Why would you even ask that? (One does not question the paradigm.) The minority of better ones then rally to come up with some reason to justify that yes, what they’re talking about can be falsified, so it does qualify as physics. But those goalposts can always be moved.

A good example of moving goalposts is the cusp-core problem. When I first encountered this in the mid to late ’90s, I tried to figure a way out of it, but failed. So I consulted one of the very best theorists, Simon White. When I asked him what he thought would constitute a falsification of cold dark matter, he said cusps: “cusps have to be there” [in the center of a dark matter halo]. Flash forward to today, when nobody would accept that as a falsification of cold dark matter: it can be fixed by feedback. Which would be fine, if it were true, which isn’t really clear. At best it provides a post facto explanation for an unpredicted phenomenon without addressing the underlying root cause, that the baryon distribution is predictive of the dynamics.

This is like putting a band-aid on a Tyrannosaurus. It’s already dead and fossilized. And if it isn’t, well, you got bigger problems.

Another disease common to theory is avoidance. A problem is first ignored, then the data are blamed for showing the wrong thing, then they are explained in a way that may or may not be satisfactory. Either way, it is treated as something that had been expected all along.

In a parallel to this gaslighting, I’ve noticed that it has become fashionable of late to describe unsatisfactory explanations as “natural.” Saying that something can be explained naturally is a powerful argument in science. The traditional meaning is that ok, we hadn’t contemplated this phenomena before it surprised us, but if we sit down and work it out, it makes sense. The “making sense” part means that an answer falls out of a theory easily when the right question is posed. If you need to run gazillions of supercomputer CPU hours of a simulation with a bunch of knobs for feedback to get something that sorta kinda approximates reality but not really, your result does not qualify as natural. It might be right – that’s a more involved adjudication – but it doesn’t qualify as natural and the current fad to abuse this term again does not inspire confidence that the results of such simulations might somehow be right. Just makes me suspect the theorists are fooling themselves.

I haven’t even talked about astroparticle physicists or those who engage in fantasies about the multiverse. I’ll just close by noting that Popper’s criterion for falsification was intended to distinguish between physics and metaphysics. That’s not the same as right or wrong, but physics is subject to experimental test while metaphysics is the stuff of late night bull sessions. The multiverse is manifestly metaphysical. Cool to think about, has lots of implications for philosophy and religion, but not physics. Even Gross has warned against treading down the garden path of the multiverse. (Tell me that you’re warning others not to make the same mistakes you made without admitting you made mistakes.)

There are a lot of scientists who would like to do away with Popper, or any requirement that physics be testable. These are inevitably the same people whose fancy turns to metascapes of mathematically beautiful if fruitless theories, and want to pass off their metaphysical ramblings as real physics. Don’t buy it.

A brief history of the Radial Acceleration Relation

In science, all new and startling facts must encounter in sequence the responses
1. It is not true!
2. It is contrary to orthodoxy.
3. We knew it all along.
Louis Agassiz (circa 1861)

This expression exactly depicts the progression of the radial acceleration relation. Some people were ahead of this curve, others are still behind it, but it quite accurately depicts the mass sociology. This is how we react to startling new facts.

For quotation purists, I’m not sure exactly what the original phrasing was. I have paraphrased it to be succinct and have substituted orthodoxy for religion, because even scientists can have orthodoxies: holy cows that must not be slaughtered.

I might even add a precursor stage zero to the list above:

0. It goes unrecognized.

This is to say, that if a new fact is sufficiently startling, we don’t just disbelieve it (stage 1); at first we fail to see it at all. We lack the cognitive framework to even recognize how important it is. An example is provided by the 1941 detection of the microwave background by Andrew McKellar. In retrospect, this is as persuasive as the 1964 detection of Penzias and Wilson to which we usually ascribe the discovery. At the earlier time, there was simply no framework for recognizing what it was that was being detected. It appears to me that P&Z didn’t know what they were looking at either until Peebles explained it to them.

The radial acceleration relation was first posed as the mass discrepancy-acceleration relation. They’re fundamentally the same thing, just plotted in a slightly different way. The mass discrepancy-acceleration relation shows the ratio of total mass to that which is visible. This is basically the ratio of the observed acceleration to that predicted by the observed baryons. This is useful to see how much dark matter is needed, but by construction the axes are not independent, as both measured quantities are used in forming the ratio.

The radial acceleration relation shows independent observations along each axis: observed vs. predicted acceleration. Though measured independently, they are not physically independent, as the baryons contribute some to the total observed acceleration – they do have mass, after all. One can construct a halo acceleration relation by subtracting the baryonic contribution away from the total; in principle the remainders are physically independent. Unfortunately, the axes again become observationally codependent, and the uncertainties blow up, especially in the baryon dominated regime. Which of these depictions is preferable depends a bit on what you’re looking to see; here I just want to note that they are the same information packaged somewhat differently.

To the best of my knowledge, the first mention of the mass discrepancy-acceleration relation in the scientific literature is by Sanders (1990). Its existence is explicit in MOND (Milgrom 1983), but here it is possible to draw a clear line between theory and data. I am only speaking of the empirical relation as it appears in the data, irrespective of anything specific to MOND.

I met Bob Sanders, along with many other talented scientists, in a series of visits to the University of Groningen in the early 1990s. Despite knowing him and having talked to him about rotation curves, I was unaware that he had done this.

Stage 0: It goes unrecognized.

For me, stage one came later in the decade at the culmination of a several years’ campaign to examine the viability of the dark matter paradigm from every available perspective. That’s a long paper, which nevertheless drew considerable praise from many people who actually read it. If you go to the bother of reading it today, you will see the outlines of many issues that are still debated and others that have been forgotten (e.g., the fine-tuning issues).

Around this time (1998), the dynamicists at Rutgers were organizing a meeting on galaxy dynamics, and asked me to be one of the speakers. I couldn’t possibly discuss everything in the paper in the time allotted, so was looking for a way to show the essence of the challenge the data posed. Consequently, I reinvented the wheel, coming up with the mass discrepancy-acceleration relation. Here I show the same data that I had then in the form of the radial acceleration relation:

*The Radial Acceleration Relation from the data in McGaugh (1999). Plot credit: Federico Lelli. (There is a time delay in publication: the 1998 meeting’s proceedings appeared in 1999.)*

I recognize this version of the plot as having been made by Federico Lelli. I’ve made this plot many times, but this is version I came across first, and it is better than mine in that the opacity of the points illustrates where the data are concentrated. I had been working on low surface brightness galaxies; these have low accelerations, so that part of the plot is well populated.

The data show a clear correlation. By today’s standards, it looks crude. Going on what we had then, it was fantastic. Correlations practically never look this good in extragalactic astronomy, and they certainly don’t happen by accident. Low quality data can hide a correlation – uncertainties cause scatter – but they can’t create a correlation where one doesn’t exist.

This result was certainly startling if not as new as I then thought. That’s why I used the title How Galaxies Don’t Form. This was contrary to our expectations, as I had explained in exhaustive detail in the long paper and revisit in a recent review for philosophers and historians of science.

I showed the same result later that year (1998) at a meeting on the campus of the University of Maryland where I was a brand new faculty member. It was a much shorter presentation, so I didn’t have time to justify the context or explain much about the data. Contrary to the reception at Rutgers where I had adequate time to speak, the hostility of the audience to the result was palpable, their stony silence eloquent. They didn’t want to believe it, and plenty of people got busy questioning the data.

Stage 1: It is not true.

I spent the next five years expanding and improving the data. More rotation curves became available thanks to the work of many, particularly Erwin de Blok, Marc Verheijen, and Rob Swaters. That was great, but the more serious limitation was how well we could measure the stellar mass distribution needed to predict the baryonic acceleration.

The mass models we could build at the time were based on optical images. A mass model takes the observed light distribution, assigns a mass-to-light ratio, and makes a numerical solution of the Poisson equation to obtain the the gravitational force corresponding to the observed stellar mass distribution. This is how we obtain the stellar contribution to the predicted baryonic force; the same procedure is applied to the observed gas distribution. The blue part of the spectrum is the best place in which to observe low contrast, low surface brightness galaxies as the night sky is darkest there, at least during new moon. That’s great for measuring the light distribution, but what we want is the stellar mass distribution. The mass-to-light ratio is expected to have a lot of scatter in the blue band simply from the happenstance of recent star formation, which makes bright blue stars that are short-lived. If there is a stochastic uptick in the star formation rate, then the mass-to-light ratio goes down because there are lots of bright stars. Wait a few hundred million years and these die off, so the mass-to-light ratio gets bigger (in the absence of further new star formation). The time-integrated stellar mass may not change much, but the amount of blue light it produces does. Consequently, we expect to see well-observed galaxies trace distinct lines in the radial acceleration plane, even if there is a single universal relation underlying the phenomenon. This happens simply because we expect to get M*/L wrong from one galaxy to the next: in 1998, I had simply assumed all galaxies had the same M*/L for lack of any better prescription. Clearly, a better prescription was warranted.

In those days, I traveled through Tucson to observe at Kitt Peak with some frequency. On one occasion, I found myself with a few hours to kill between coming down from the mountain and heading to the airport. I wandered over to the Steward Observatory at the University of Arizona to see who I might see. A chance meeting in the wild west: I encountered Eric Bell and Roelof de Jong, who were postdocs there at the time. I knew Eric from his work on the stellar populations of low surface brightness galaxies, an interest closely aligned with my own, and Roelof from my visits to Groningen.

As we got to talking, Eric described to me work they were doing on stellar populations, and how they thought it would be possible to break the age-metallicity degeneracy using near-IR colors in addition to optical colors. They were mostly focused on improving the age constraints on stars in LSB galaxies, but as I listened, I realized they had constructed a more general, more powerful tool. At my encouragement (read their acknowledgements), they took on this more general task, ultimately publishing the classic Bell & de Jong (2001). In it, they built a table that enabled one to look up the expected mass-to-light ratio of a complex stellar population – one actively forming stars – as a function of color. This was a big step forward over my educated guess of a constant mass-to-light ratio: there was now a way to use a readily observed property, color, to improve the estimated M*/L of each galaxy in a well-calibrated way.

Combining the new stellar population models with all the rotation curves then available, I obtained an improved mass discrepancy-acceleration relation:

The Radial Acceleration Relation from the data in McGaugh (2004); version using Bell’s stellar population synthesis models to estimate M*/L (see Fig. 5 for other versions). Plot credit: Federico Lelli.

Again, the relation is clear, but with scatter. Even with the improved models of Bell & de Jong, some individual galaxies have M*/L that are wrong – that’s inevitable in this game. What you cannot know is which ones! Note, however, that there are now 74 galaxies in this plot, and almost all of them fall on top of each other where the point density is large. There are some obvious outliers; those are presumably just that: the trees that fall outside the forest because of the expected scatter in M*/L estimates.

I tried a variety of prescriptions for M*/L in addition to that of Bell & de Jong. Though they differed in texture, they all told a consistent story. A relation was clearly present; only its detailed form varied with the adopted prescription.

The prescription that minimized the scatter in the relation was the M*/L obtained in MOND fits. That’s a tautology: by construction, a MOND fit finds the M*/L that puts a galaxy on this relation. However, we can generalize the result. Maybe MOND is just a weird, unexpected way of picking a number that has this property; it doesn’t have to be the true mass-to-light ratio in nature. But one can then define a ratio Q

that relates the “true” mass-to-light ratio to the number that gives a MOND fit. They don’t have to be identical, but MOND does return M*/L that are reasonable in terms of stellar populations, so Q ~ 1. Individual values could vary, and the mean could be a bit more or less than unity, but not radically different. One thing that impressed me at the time about the MOND fits (most of which were made by Bob Sanders) was how well they agreed with the stellar population models, recovering the correct amplitude, the correct dependence on color in different bandpasses, and also giving the expected amount of scatter (more in the blue than in the near-IR).

Fig. 7 *of McGaugh (2004).* Stellar mass-to-light ratios of galaxies in the blue B-band (*top*) and near-IR K-band (*bottom*) as a function of B–V color for the prescription of maximum disk (*left*) and MOND (*right*). Each point represents one galaxy for which the requisite data were available at the time. The line represents the mean expectation of stellar population synthesis models from Bell et al. (2003). These lines are completely independent of the data: neither the normalization nor the slope has been fit to the dynamical data. The red points are due to Sanders & Verheijen (1998); note the weak dependence of M*/L on color in the near-IR.

The obvious interpretation is that we should take seriously a theory that obtains good fits with a single free parameter that checks out admirably well with independent astrophysical constraints, in this case the M*/L expected for stellar populations. But I knew many people would not want to do that, so I defined Q to generalize to any M*/L in any (dark matter) context one might want to consider.

Indeed, Q allows us to write a general expression for the rotation curve of the dark matter halo (essentially the HAR alluded to above) in terms of that of the stars and gas:

Equation 22 of McGaugh (2004).

The stars and the gas are observed, and μ is the MOND interpolation function assumed in the fit that leads to Q. Except now the interpolation function isn’t part of some funny new theory; it is just the shape of the radial acceleration relation – a relation that is there empirically. The only fit factor between these data and any given model is Q – a single number of order unity. This does leave some wiggle room, but not much.

I went off to a conference to describe this result. At the 2006 meeting Galaxies in the Cosmic Web in New Mexico, I went out of my way at the beginning of the talk to show that even if we ignore MOND, this relation is present in the data, and it provides a strong constraint on the required distribution of dark matter. We may not know why this relation happens, but we can use it, modulo only the modest uncertainty in Q.

Having bent over backwards to distinguish the data from the theory, I was disappointed when, immediately at the end of my talk, prominent galaxy formation theorist Anatoly Klypin loudly shouted

“We don’t have to explain MOND!”

But you do have to explain the data. The problem was and is that the data look like MOND. It is easy to conflate one with the other; I have noticed that a lot of people have trouble keeping the two separate. Just because you don’t like the theory doesn’t mean that the data are wrong. What Anatoly was saying was that

2. It is contrary to orthodoxy.

Despite phrasing the result in a way that would be useful to galaxy formation theorists, they did not, by and large, claim to explain it at the time – it was contrary to orthodoxy so didn’t need to be explained. Looking at the list of papers that cite this result, the early adopters were not the target audience of galaxy formation theorists, but rather others citing it to say variations of “no way dark matter explains this.”

At this point, it was clear to me that further progress required a better way to measure the stellar mass distribution. Looking at the stellar population models, the best hope was to build mass models from near-infrared rather than optical data. The near-IR is dominated by old stars, especially red giants. Galaxies that have been forming stars actively for a Hubble time tend towards a quasi-equilibrium in which red giants are replenished by stellar evolution at about the same rate they move on to the next phase. One therefore expects the mass-to-light ratio to be more nearly constant in the near-IR. Not perfectly so, of course, but a 2 or 3 micron image is as close to a map of the stellar mass of a galaxy as we’re likely to get.

Around this time, the University of Maryland had begun a collaboration with Kitt Peak to build a big infrared camera, NEWFIRM, for the 4m telescope. Rob Swaters was hired to help write software to cope with the massive data flow it would produce. The instrument was divided into quadrants, each of which had a field of view sufficient to hold a typical galaxy. When it went on the telescope, we developed an efficient observing method that I called “four-shooter”, shuffling the target galaxy from quadrant to quadrant so that in processing we could remove the numerous instrumental artifacts intrinsic to its InSb detectors. This eventually became one of the standard observing modes in which the instrument was operated.

NEWFIRM in the lab in Tucson. Most of the volume is for cryogenics: the IR detectors are *helium*–*cooled to 30 K. Partial student for scale.*

I was optimistic that we could make rapid progress, and at first we did. But despite all the work, despite all the active cooling involved, we were still on the ground. The night sky was painfully bright in the IR. Indeed, the thermal component dominated, so we could observe during full moon. To an observer of low surface brightness galaxies attuned to any hint of scattered light from so much as a crescent moon, I cannot describe how discombobulating it was to walk outside the dome and see the full fricking moon. So bright. So wrong. And that wasn’t even the limiting factor: the thermal background was.

We had hit a surface brightness wall, again. We could do the bright galaxies this way, but the LSBs that sample the low acceleration end of the radial acceleration relation were rather less accessible. Not inaccessible, but there was a better way.

The Spitzer Space Telescope was active at this time. Jim Schombert and I started winning time to observe LSB galaxies with it. We discovered that space is dark. There was no atmosphere to contend with. No scattered light from the clouds or the moon or the OH lines that afflict that part of the sky spectrum. No ground-level warmth. The data were fantastic. In some sense, they were too good: the biggest headache we faced was blotting out all the background galaxies that shown right through the optically thin LSB galaxies.

Still, it took a long time to collect and analyze the data. We were starting to get results by the early-teens, but it seemed like it would take forever to get through everything I hoped to accomplish. Fortunately, when I moved to Case Western, I was able to hire Federico Lelli as a postdoc. Federico’s involvement made all the difference. After many months of hard, diligent, and exacting work, he constructed what is now the SPARC database. Finally all the elements were in place to construct an empirical radial acceleration relation with absolutely minimal assumptions about the stellar mass-to-light ratio.

In parallel with the observational work, Jim Schombert had been working hard to build realistic stellar population models that extended to the 3.6 micron band of Spitzer. Spitzer had been built to look redwards of this, further into the IR. 3.6 microns was its shortest wavelength passband. But most models at the time stopped at the K-band, the 2.2 micron band that is the reddest passband that is practically accessible from the ground. They contain pretty much the same information, but we still need to calculate the band-specific value of M*/L.

Being a thorough and careful person, Jim considered not just the star formation history of a model stellar population as a variable, and not just its average metallicity, but also the metallicity distribution of its stars, making sure that these were self-consistent with the star formation history. Realistic metallicity distributions are skewed; it turn out that this subtle effect tends to counterbalance the color dependence of the age effect on M*/L in the near-IR part of the spectrum. The net results is that we expect M*/L to be very nearly constant for all late type galaxies.

This is the best possible result. To a good approximation, we expected all of the galaxies in the SPARC sample to have the same mass-to-light ratio. What you see is what you get. No variable M*/L, no equivocation, just data in, result out.

We did still expect some scatter, as that is an irreducible fact of life in this business. But even that we expected to be small, between 0.1 and 0.15 dex (roughly 25 – 40%). Still, we expected the occasional outlier, galaxies that sit well off the main relation just because our nominal M*/L didn’t happen to apply in that case.

One day as I walked past Federico’s office, he called for me to come look at something. He had plotted all the data together assuming a single M*/L. There… were no outliers. The assumption of a constant M*/L in the near-IR didn’t just work, it worked far better than we had dared to hope. The relation leapt straight out of the data:

*The Radial Acceleration Relation from the data in McGaugh et al. (2016)*. Plot credit: Federico Lelli.

Over 150 galaxies, with nearly 2700 resolved measurements within each galaxy, each with their own distinctive mass distribution, all pile on top of each other without effort. There was plenty of effort in building the database, but once it was there, the result appeared, no muss, no fuss. No fitting or fiddling. Just the measurements and our best estimate of the mean M*/L, applied uniformly to every individual galaxy in the sample. The scatter was only 0.12 dex, within the range expected from the population models.

No MOND was involved in the construction of this relation. It may look like MOND, but we neither use MOND nor need it in any way to see the relation. It is in the data. Perhaps this is the sort of result for which we would have to invent MOND if it did not already exist. But the dark matter paradigm is very flexible, and many papers have since appeared that claim to explain the radial acceleration relation. We have reached

3. We knew it all along.

On the one hand, this is good: the community is finally engaging with a startling fact that has been pointedly ignored for decades. On the other hand, many of the claims to explain the radial acceleration relation are transparently incorrect on their face, being nothing more than elaborations of models I considered and discarded as obviously unworkable long ago. They do not provide a satisfactory explanation of the predictive power of MOND, and inevitably fail to address important aspects of the problem, like disk stability. Rather than grapple with the deep issues the new and startling fact poses, it has become fashionable to simply assert that one’s favorite model explains the radial acceleration relation, and does so naturally.

There is nothing natural about the radial acceleration relation in the context of dark matter. Indeed, it is difficult to imagine a less natural result – hence stages one and two. So on the one hand, I welcome the belated engagement, and am willing to consider serious models. On the other hand, if someone asserts that this is natural and that we expected it all along, then the engagement isn’t genuine: they’re just fooling themselves.

Early Days. This was one of Vera Rubin’s favorite expressions. I always had a hard time with it, as many things are very well established. Yet it seems that we have yet to wrap our heads around the problem. Vera’s daughter, Judy Young, once likened the situation to the parable of the blind men and the elephant. Much is known, yes, but the problem is so vast that each of us can perceive only a part of the whole, and the whole may be quite different from the part that is right before us.

So I guess Vera is right as always: these remain Early Days.

A script for every observational test

Science progresses through hypothesis testing. The primary mechanism for distinguishing between hypotheses is predictive power. The hypothesis that can predict new phenomena is “better.” This is especially true for surprising, a priori predictions: it matters more when the new phenomena was not expected in the context of an existing paradigm.

I’ve seen this happen many times now. MOND has had many predictive successes. As a theory, it has been exposed to potential falsification, and passed many tests. These have often been in the form of phenomena that had not been anticipated in any other way, and were initially received as strange to the point of seeming impossible. It is exactly the situation envisioned in Putnam’s “no miracles” argument: it is unlikely to the point of absurdity that a wholly false theory should succeed in making so many predictions of such diversity and precision.

MOND has many doubters, which I can understand. What I don’t get is the ignorance I so often encounter among them. To me, the statement that MOND has had many unexpected predictions come true is a simple statement of experiential fact. I suspect it will be received by some as a falsehood. It shouldn’t be, so if you don’t know what I’m talking about, you should try reading the relevant literature. What papers about MOND have you actually read?

Ignorance is not a strong basis for making scientific judgements. Before I criticize something, I make sure I know what I’m talking about. That’s rarely true of the complaints I hear against MOND. There are legitimate ones, to be sure, but for the most part I hear assertions like

MOND is guaranteed to fit rotation curves.
It fits rotation curves but does nothing else.
It is just a fitting tool with no predictive power.

These are myths, plain and simple. They are easily debunked, and were long ago. Yet I hear them repeated often by people who think they know better, one as recently as last week. Serious people who expect to be taken seriously as scientists, and yet they repeat known falsehoods as if they were established fact. Is there a recycling bin of debunked myths that gets passed around? I guess it is easy to believe a baseless rumor when it conforms to your confirmation bias: no need for fact-checking!

Aside from straight-up reality denial, another approach is to claim that dark matter predicts exactly the same thing, whatever it is. I’ve seen this happen so often, I know how the script always goes:

• We make a new observation X that is surprising.
• We test the hypothesis, and report the result: “Gee, MOND predicted this strange effect, and we see evidence of it in the data.”
• Inevitable Question: What does LCDM predict?
• Answer: Not that.
• Q: But what does it predict?
• A: It doesn’t really make a clear prediction on this subject, so we have to build some kind of model to even begin to address this question. In the most obvious models one can construct, it predicts Y. Y is not the same as X.
• Q: What about more complicated models?
• A: One can construct more complicated models, but they are not unique. They don’t make a prediction so much as provide a menu of options from which we may select the results that suit us. The obvious danger is that it becomes possible to do anything, and we have nothing more than an epicycle theory of infinite possibilities. If we restrict ourselves to considering the details of serious models that have only been partially fine-tuned over the course of the development of the field, then there are still a lot of possibilities. Some of them come closer to reality than others but still don’t really do the right thing for the following reasons…[here follows 25 pages of minutia in the ApJ considering every up/down left/right stand on your head and squint possibility that still winds up looking more like Y than like X.] You certainly couldn’t predict X this way, as MOND did a priori.
• Q: That’s too long to read. Dr. Z says it works, so he must be right since we already know that LCDM is correct.

The thing is, Dr. Z did not predict X ahead of time. MOND did. Maybe Dr. Z’s explanation in terms of dark matter makes sense. Often it does not, but even if it does, so what? Why should I be more impressed with a theory that only explains things after they’re observed when another predicted them a priori?

There are lots of Dr. Z’s. No matter how carefully one goes through the minutia, no matter how clearly one demonstrates that X cannot work in a purely conventional CDM context, there is always someone who says it does. That’s what people want to hear, so that’s what they choose to believe. Way easier that way. Or, as it has been noted before

Faced with the choice between changing one’s mind and proving that there is no need to do so, almost everybody gets busy on the proof.
J. K. Galbraith (1965)

The curious case of AGC 114905: an isolated galaxy devoid of dark matter?

It’s early in the new year, so what better time to violate my own resolutions? I prefer to be forward-looking and not argue over petty details, or chase wayward butterflies. But sometimes the devil is in the details, and the occasional butterfly can be entertaining if distracting. Today’s butterfly is the galaxy AGC 114905, which has recently been in the news.

There are a couple of bandwagons here: one to rebrand very low surface brightness galaxies as ultradiffuse, and another to get overly excited when these types of galaxies appear to lack dark matter. The nomenclature is terrible, but that’s normal for astronomy so I would overlook it, except that in this case it gives the impression that there is some new population of galaxies behaving in an unexpected fashion, when instead it looks to me like the opposite is the case. The extent to which there are galaxies lacking dark matter is fundamental to our interpretation of the acceleration discrepancy (aka the missing mass problem), so bears closer scrutiny. The evidence for galaxies devoid of dark matter is considerably weaker than the current bandwagon portrays.

If it were just one butterfly (e.g., NGC 1052-DF2), I wouldn’t bother. Indeed, it was that specific case that made me resolve to ignore such distractions as a waste of time. I’ve seen this movie literally hundreds of times, I know how it goes:

Observations of this one galaxy falsify MOND!
Hmm, doing the calculation right, that’s what MOND predicts.
OK, but better data shrink the error bars and now MOND falsified.
Are you sure about…?
Yes. We like this answer, let’s stop thinking about it now.
As the data continue to improve, it approaches what MOND predicts.
<crickets>

Over and over again. DF44 is another example that has followed this trajectory, and there are many others. This common story is not widely known – people lose interest once they get the answer they want. Irrespective of whether we can explain this weird case or that, there is a deeper story here about data analysis and interpretation that seems not to be widely appreciated.

My own experience inevitably colors my attitude about this, as it does for us all, so let’s start thirty years ago when I was writing a dissertation on low surface brightness (LSB) galaxies. I did many things in my thesis, most of them well. One of the things I tried to do then was derive rotation curves for some LSB galaxies. This was not the main point of the thesis, and arose almost as an afterthought. It was also not successful, and I did not publish the results because I didn’t believe them. It wasn’t until a few years later, with improved data, analysis software, and the concerted efforts of Erwin de Blok, that we started to get a handle on things.

The thing that really bugged me at the time was not the Doppler measurements, but the inclinations. One has to correct the observed velocities by the inclination of the disk, 1/sin(i). The inclination can be constrained by the shape of the image and by the variation of velocities across the face of the disk. LSB galaxies presented raggedy images and messy velocity fields. I found it nigh on impossible to constrain their inclinations at the time, and it remains a frequent struggle to this day.

Here is an example of the LSB galaxy F577-V1 that I find lurking around on disk from all those years ago:

*The LSB galaxy F577-V1 (B-band image, left) and the run of the eccentricity of ellipses fit to the atomic gas data (right).*

A uniform disk projected on the sky at some inclination will have a fixed corresponding eccentricity, with zero being the limit of a circular disk seen perfectly face-on (i = 0). Do you see a constant value of the eccentricity in the graph above? If you say yes, go get your eyes checked.

What we see in this case is a big transition from a fairly eccentric disk to one that is more nearly face on. The inclination doesn’t have a sudden warp; the problem is that the assumption of a uniform disk is invalid. This galaxy has a bar – a quasi-linear feature that is common in many spiral galaxies that is supported by non-circular orbits. Even face-on, the bar will look elongated simply because it is. Indeed, the sudden change in eccentricity is one way to define the end of the bar, which the human eye-brain can do easily by looking at the image. So in a case like this, one might adopt the inclination from the outer points, and that might even be correct. But note that there are spiral arms along the outer edge that is visible to the eye, so it isn’t clear that even these isophotes are representative of the shape of the underlying disk. Worse, we don’t know what happens beyond the edge of the data; the shape might settle down at some other level that we can’t see.

This was so frustrating, I swore never to have anything to do with galaxy kinematics ever again. Over 50 papers on the subject later, all I can say is D’oh! Repeatedly.

Bars are rare in LSB galaxies, but it struck me as odd that we saw any at all. We discovered unexpectedly that they were dark matter dominated – the inferred dark halo outweighs the disk, even within the edge defined by the stars – but that meant that the disks should be stable against the formation of bars. My colleague Chris Mihos agreed, and decided to look into it. The answer was yes, LSB galaxies should be stable against bar formation, at least internally generated bars. Sometimes bars are driven by external perturbations, so we decided to simulate the close passage of a galaxy of similar mass – basically, whack it real hard and see what happens:

Simulation of an LSB galaxy during a strong tidal encounter with another galaxy. Closest approach is at t=24 in simulation units (between the first and second box). A linear bar does not form, but the model galaxy does suffer a strong and persistent oval distortion: all these images are shown face-on (i=0). From Mihos et al (1997).

This was a conventional simulation, with a dark matter halo constructed to be consistent with the observed properties of the LSB galaxy UGC 128. The results are not specific to this case; it merely provides numerical corroboration of the more general case that we showed analytically.

Consider the image above in the context of determining galaxy inclinations from isophotal shapes. We know this object is face-on because we can control our viewing angle in the simulation. However, we would not infer i=0 from this image. If we didn’t know it had been perturbed, we would happily infer a substantial inclination – in this case, easily as much as 60 degrees! This is an intentionally extreme case, but it illustrates how a small departure from a purely circular shape can be misinterpreted as an inclination. This is a systematic error, and one that usually makes the inclination larger than it is: it is possible to appear oval when face-on, but it is not possible to appear more face-on than perfectly circular.

Around the same time, Erwin and I were making fits to the LSB galaxy data – with both dark matter halos and MOND. By this point in my career, I had deeply internalized that the data for LSB galaxies were never perfect. So we sweated every detail, and worked through every “what if?” This was a particularly onerous task for the dark matter fits, which could do many different things if this or that were assumed – we discussed all the plausible possibilities at the time. (Subsequently, a rich literature sprang up discussing many unreasonable possibilities.) By comparison, the MOND fits were easy. They had fewer knobs, and in 2/3 of the cases they simply worked, no muss, no fuss.

For the other 1/3 of the cases, we noticed that the shape of the MOND-predicted rotation curves was usually right, but the amplitude was off. How could it work so often, and yet miss in this weird way? That sounded like a systematic error, and the inclination was the most obvious culprit, with 1/sin(i) making a big difference for small inclinations. So we decided to allow this as a fit parameter, to see whether a fit could be obtained, and judge how [un]reasonable this was. Here is an example for two galaxies:

UGC 1230 (left) and UGC 5005 (right). Ovals show the nominally measured inclination (i=22^o for UGC 1230 and 41^o for UGC 5005, respectively) and the MOND best-fit value (i=17^o and 30^o). From de Blok & McGaugh (1998).

The case of UGC 1230 is memorable to me because it had a good rotation curve, despite being more face-on than widely considered acceptable for analysis. And for good reason: the difference between 22 and 17 degrees make a huge difference to the fit, changing it from way off to picture perfect.

*Rotation curve fits for UGC 1230 (top) and UGC 5005 (bottom) with the inclination fixed (left) and fit (right). From de Blok & McGaugh (1998).*

What I took away from this exercise is how hard it is to tell the difference between inclination values for relatively face-on galaxies. UGC 1230 is obvious: the ovals for the two inclinations are practically on top of each other. The difference in the case of UGC 5005 is more pronounced, but look at the galaxy. The shape of the outer isophote where we’re trying to measure this is raggedy as all get out; this is par for the course for LSB galaxies. Worse, look further in – this galaxy has a bar! The central bar is almost orthogonal to the kinematic major axis. If we hadn’t observed as deeply as we had, we’d think the minor axis was the major axis, and the inclination was something even higher.

I remember Erwin quipping that he should write a paper on how to use MOND to determine inclinations. This was a joke between us, but only half so: using the procedure in this way would be analogous to using Tully-Fisher to measure distances. We would simply be applying an empirically established procedure to constrain a property of a galaxy – luminosity from line-width in that case of Tully-Fisher; inclination from rotation curve shape here. That we don’t understand why this works has never stopped astronomers before.

Systematic errors in inclination happen all the time. Big surveys don’t have time to image deeply – they have too much sky area to cover – and if there is follow-up about the gas content, it inevitably comes in the form of a single dish HI measurement. This is fine; it is what we can do en masse. But an unresolved single dish measurement provides no information about the inclination, only a pre-inclination line-width (which itself is a crude proxy for the flat rotation speed). The inclination we have to take from the optical image, which would key on the easily detected, high surface brightness central region of the image. That’s the part that is most likely to show a bar-like distortion, so one can expect lots of systematic errors in the inclinations determined in this way. I provided a long yet still incomplete discussion of these issues in McGaugh (2012). This is both technical and intensely boring, so not even the pros read it.

This brings us to the case of AGC 114905, which is part of a sample of ultradiffuse galaxies discussed previously by some of the same authors. On that occasion, I kept to the code, and refrained from discussion. But for context, here are those data on a recent Baryonic Tully-Fisher plot. Spoiler alert: that post was about a different sample of galaxies that seemed to be off the relation but weren’t.

Baryonic Tully-Fisher relation showing the ultradiffuse galaxies discussed by Mancera Piña et al. (2019) as gray circles. These are all outliers from the relation; AGC 114905 is highlighted in orange. Placing much meaning in the outliers is a classic case of missing the forest for the trees. The outliers are trees. The Tully-Fisher relation is the forest.

On the face of it, these ultradiffuse galaxies (UDGs) are all very serious outliers. This is weird – they’re not some scatter off to one side, they’re just way off on their own island, with no apparent connection to the rest of established reality. By calling them a new name, UDG, it makes it sound plausible that these are some entirely novel population of galaxies that behave in a new way. But they’re not. They are exactly the same kinds of galaxies I’ve been talking about. They’re all blue, gas rich, low surface brightness, fairly isolated galaxies – all words that I’ve frequently used to describe my thesis sample. These UDGs are all a few billion solar mass is baryonic mass, very similar to F577-V1 above. You could give F577-V1 a different name, slip into the sample, and nobody would notice that it wasn’t like one of the others.

The one slight difference is implied by the name: UDGs are a little lower in surface brightness. Indeed, once filter transformations are taken into account, the definition of ultradiffuse is equal to what I arbitrarily called very low surface brightness in 1996. Most of my old LSB sample galaxies have central stellar surface brightnesses at or a bit above 10 solar masses per square parsec while the UDGs here are a bit under this threshold. For comparison, in typical high surface brightness galaxies this quantity is many hundreds, often around a thousand. Nothing magic happens at the threshold of 10 solar masses per square parsec, so this line of definition between LSB and UDG is an observational distinction without a physical difference. So what are the odds of a different result for the same kind of galaxies?

Indeed, what really matters is the baryonic surface density, not just the stellar surface brightness. A galaxy made purely of gas but no stars would have zero optical surface brightness. I don’t know of any examples of that extreme, but we came close to it with the gas rich sample of Trachternach et al. (2009) when we tried this exact same exercise a decade ago. Despite selecting that sample to maximize the chance of deviations from the Baryonic Tully-Fisher relation, we found none – at least none that were credible: there were deviant cases, but their data were terrible. There were no deviants among the better data. This sample is comparable or even extreme than the UDGs in terms of baryonic surface density, so the UDGs can’t be exception because they’re a genuinely new population, whatever name we call them by.

The key thing is the credibility of the data, so let’s consider the data for AGC 114905. The kinematics are pretty well ordered; the velocity field is well observed for this kind of beast. It ought to be; they invested over 40 hours of JVLA time into this one galaxy. That’s more than went into my entire LSB thesis sample. The authors are all capable, competent people. I don’t think they’ve done anything wrong, per se. But they do seem to have climbed aboard the bandwagon of dark matter-free UDGs, and have talked themselves into believing smaller error bars on the inclination than I am persuaded is warranted.

Here is the picture of AGC 114905 from Mancera Piña et al. (2021):

AGC 114905 in stars (left) and gas (right). The contours of the gas distribution are shown on top of the stars in white. Figure 1 from Mancera Piña et al. (2021).

This messy morphology is typical of very low surface brightness galaxies – hence their frequent classification as Irregular galaxies. Though messier, it shares some morphological traits with the LSB galaxies shown above. The central light distribution is elongated with a major axis that is not aligned with that of the gas. The gas is raggedy as all get out. The contours are somewhat boxy; this is a hint that something hinky is going on beyond circular motion in a tilted axisymmetric disk.

The authors do the right thing and worry about the inclination, checking to see what it would take to be consistent with either LCDM or MOND, which is about i=11^o in stead of the 30^o indicated by the shape of the outer isophote. They even build a model to check the plausibility of the smaller inclination:

*Contours of models of disks with different inclinations (lines, as labeled) compared to the outer contour of the gas distribution of AGC 114905. Figure 7 from Mancera Piña et al. (2021).*

Clearly the black line (i=30^o) is a better fit to the shape of the gas distribution than the blue dashed line (i=11^o). Consequently, they “find it unlikely that we are severely overestimating the inclination of our UDG, although this remains the largest source of uncertainty in our analysis.” I certainly agree with the latter phrase, but not the former. I think it is quite likely that they are overestimating the inclination. I wouldn’t even call it a severe overestimation; more like par for the course with this kind of object.

As I have emphasized above and elsewhere, there are many things that can go wrong in this sort of analysis. But if I were to try to put my finger on the most important thing, here it would be the inclination. The modeling exercise is good, but it assumes “razor-thin axisymmetric discs.” That’s a reasonable thing to do when building such a model, but we have to bear in mind that real disks are neither. The thickness of the disk probably doesn’t matter too much for a nearly face-on case like this, but the assumption of axisymmetry is extraordinarily dubious for an Irregular galaxy. That’s how they got the name.

It is hard to build models that are not axisymmetric. Once you drop this simplifying assumption, where do you even start? So I don’t fault them for stopping at this juncture, but I can also imagine doing as de Blok suggested, using MOND to set the inclination. Then one could build models with asymmetric features by trial and error until a match is obtained. Would we know that such a model would be a better representation of reality? No. Could we exclude such a model? Also no. So the bottom line is that I am not convinced that the uncertainty in the inclination is anywhere near as small as the adopted ±3^o.

That’s very deep in the devilish details. If one is worried about a particular result, one can back off and ask if it makes sense in the context of what we already know. I’ve illustrated this process previously. First, check the empirical facts. Every other galaxy in the universe with credible data falls on the Baryonic Tully-Fisher relation, including very similar galaxies that go by a slightly different name. Hmm, strike one. Second, check what we expect from theory. I’m not a fan of theory-informed data interpretation, but we know that LCDM, unlike SCDM before it, at least gets the amplitude of the rotation speed in the right ballpark (V_flat ~ V₂₀₀). Except here. Strike two. As much as we might favor LCDM as the standard cosmology, it has now been extraordinarily well established that MOND has considerable success in not just explaining but predicting these kind of data, with literally hundreds of examples. One hundred was the threshold Vera Rubin obtained to refute excuses made to explain away the first few flat rotation curves. We’ve crossed that threshold: MOND phenomenology is as well established now as flat rotation curves were at the inception of the dark matter paradigm. So while I’m open to alternative explanations for the MOND phenomenology, seeing that a few trees stand out from the forest is never going to be as important as the forest itself.

The Baryonic Tully-Fisher relation exists empirically; we have to explain it in any theory. Either we explain it, or we don’t. We can’t have it both ways, just conveniently throwing away our explanation to accommodate any discrepant observation that comes along. That’s what we’d have to do here: if we can explain the relation, we can’t very well explain the outliers. If we explain the outliers, it trashes our explanation for the relation. If some galaxies are genuine exceptions, then there are probably exceptional reasons for them to be exceptions, like a departure from equilibrium. That can happen in any theory, rendering such a test moot: a basic tenet of objectivity is that we don’t get to blame a missed prediction of LCDM on departures from equilibrium without considering the same possibility for MOND.

This brings us to a physical effect that people should be aware of. We touched on the bar stability above, and how a galaxy might look oval even when seen face on. This happens fairly naturally in MOND simulations of isolated disk galaxies. They form bars and spirals and their outer parts wobble about. See, for example, this simulation by Nils Wittenburg. This particular example is a relatively massive galaxy; the lopsidedness reminds me of M101 (Watkins et al. 2017). Lower mass galaxies deeper in the MOND regime are likely even more wobbly. This happens because disks are only marginally stable in MOND, not the over-stabilized entities that have to be hammered to show a response as in our early simulation of UGC 128 above. The point is that there is good reason to expect even isolated face-on dwarf Irregulars to look, well, irregular, leading to exactly the issues with inclination determinations discussed above. Rather than being a contradiction to MOND, AGC 114905 may illustrate one of its inevitable consequences.

I don’t like to bicker at this level of detail, but it makes a profound difference to the interpretation. I do think we should be skeptical of results that contradict well established observational reality – especially when over-hyped. God knows I was skeptical of our own results, which initially surprised the bejeepers out of me, but have been repeatedly corroborated by subsequent observations.

I guess I’m old now, so I wonder how I come across to younger practitioners; perhaps as some scary undead monster. But mates, these claims about UDGs deviating from established scaling relations are off the edge of the map.

Super spirals on the Tully-Fisher relation

A surprising and ultimately career-altering result that I encountered while in my first postdoc was that low surface brightness galaxies fell precisely on the Tully-Fisher relation. This surprising result led me to test the limits of the relation in every conceivable way. Are there galaxies that fall off it? How far is it applicable? Often, that has meant pushing the boundaries of known galaxies to ever lower surface brightness, higher gas fraction, and lower mass where galaxies are hard to find because of unavoidable selection biases in galaxy surveys: dim galaxies are hard to see.

I made a summary plot in 2017 to illustrate what we had learned to that point. There is a clear break in the stellar mass Tully-Fisher relation (left panel) that results from neglecting the mass of interstellar gas that becomes increasingly important in lower mass galaxies. The break goes away when you add in the gas mass (right panel). The relation between baryonic mass and rotation speed is continuous down to Leo P, a tiny galaxy just outside the Local Group comparable in mass to a globular cluster and the current record holder for the slowest known rotating galaxy at a mere 15 km/s.

The stellar mass (left) and baryonic (right) Tully-Fisher relations constructed in 2017 from SPARC data and gas rich galaxies. Dark blue points are star dominated galaxies; light blue points are galaxies with more mass in gas than in stars. The data are restricted to galaxies with distance measurements accurate to 20% or better; *see McGaugh et al. (2019)* for a discussion of the effects of different quality criteria. The line has a slope of 4 and is identical in both panels for comparison.

At the high mass end, galaxies aren’t hard to see, but they do become progressively rare: there is an exponential cut off in the intrinsic numbers of galaxies at the high mass end. So it is interesting to see how far up in mass we can go. Ogle et al. set out to do that, looking over a huge volume to identify a number of very massive galaxies, including what they dubbed “super spirals.” These extend the Tully-Fisher relation to higher masses.

*The Tully-Fisher relation extended to very massive “super” spirals (blue points) by Ogle et al. (2019).*

Most of the super spirals lie on the top end of the Tully-Fisher relation. However, a half dozen of the most massive cases fall off to the right. Could this be a break in the relation? So it was claimed at the time, but looking at the data, I wasn’t convinced. It looked to me like they were not always getting out to the flat part of the rotation curve, instead measuring the maximum rotation speed.

Bright galaxies tend to have rapidly rising rotation curves that peak early then fall before flattening out. For very bright galaxies – and super spirals are by definition the brightest spirals – the amplitude of the decline can be substantial, several tens of km/s. So if one measures the maximum speed instead of the flat portion of the curve, points will fall to the right of the relation. I decided not to lose any sleep over it, and wait for better data.

Better data have now been provided by Di Teodoro et al. Here is an example from their paper. The morphology of the rotation curve is typical of what we see in massive spiral galaxies. The maximum rotation speed exceeds 300 km/s, but falls to 275 km/s where it flattens out.

*A super spiral (left) and its rotation curve (right) from Di Teodoro et al.*

Adding the updated data to the plot, we see that the super spirals now fall on the Tully-Fisher relation, with no hint of a break. There are a couple of outliers, but those are trees. The relation is the forest.

*The super spiral (red points) stellar mass (left) and baryonic (right) Tully-Fisher relations as updated by Di Teodoro et al. (2021).*

That’s a good plot, but it stops at 10⁸ solar masses, so I couldn’t resist adding the super spirals to my plot from 2017. I’ve also included the dwarfs I discussed in the last post. Together, we see that the baryonic Tully-Fisher relation is continuous over six decades in mass – a factor of million from the smallest to the largest galaxies.

The plot from above updated to include the super spirals (red points) at high mass and Local Group dwarfs (gray squares) at low mass. The SPARC data (blue points) have also been updated with new stellar population mass-to-light ratio estimates that make their bulge components a bit more massive, and with scaling relations for metallicity and molecular gas. The super spirals have been treated in the same way, and adjusted to a matching distance scale (H₀ = 73 km/s/Mpc). There is some overlap between the super spirals and the most massive galaxies in SPARC; here the data are in excellent agreement. The super spirals extend to higher mass by a factor of two.

The strength of this correlation continues to amaze me. This never happens in extragalactic astronomy, where correlations are typically weak and have lots of intrinsic scatter. The opposite is true here. This must be telling us something.

The obvious thing that this is telling us is MOND. The initial report that super spirals fell off of the Tully-Fisher relation was widely hailed as a disproof of MOND. I’ve seen this movie many times, so I am not surprised that the answer changed in this fashion. It happens over and over again. Even less surprising is that there is no retraction, no self-examination of whether maybe we jumped to the wrong conclusion.

I get it. I couldn’t believe it myself, to start. I struggled for many years to explain the data conventionally in terms of dark matter. Worked my ass off trying to save the paradigm. Try as I might, nothing worked. Since then, many people have claimed to explain what I could not, but so far all I have seen are variations on models that I had already rejected as obviously unworkable. They either make unsubstantiated assumptions, building a tautology, or simply claim more than they demonstrate. As long as you say what people want to hear, you will be held to a very low standard. If you say what they don’t want to hear, what they are conditioned not to believe, then no standard of proof is high enough.

MOND was the only theory to predict the observed behavior a priori. There are no free parameters in the plots above. We measure the mass and the rotation speed. The data fall on the predicted line. Dark matter models did not predict this, and can at best hope to provide a convoluted, retroactive explanation. Why should I be impressed by that?

Divergence

I read somewhere – I don’t think it was Kuhn himself, but someone analyzing Kuhn – that there came a point in the history of science where there was a divergence between scientists, with different scientists disagreeing about what counts as a theory, what counts as a test of a theory, what even counts as evidence. We have reached that point with the mass discrepancy problem.

For many years, I worried that if the field ever caught up with me, it would zoom past. That hasn’t happened. Instead, it has diverged towards a place that I barely recognize as science. It looks more like the Matrix – a simulation – that is increasingly sophisticated yet self-contained, making only parsimonious contact with observational reality and unable to make predictions that apply to real objects. Scaling relations and statistical properties, sure. Actual galaxies with NGC numbers, not so much. That, to me, is not science.

I have found it increasingly difficult to communicate across the gap built on presumptions buried so deep that they cannot be questioned. One obvious one is the existence of dark matter. This has been fueled by cosmologists who take it for granted and particle physicists eager to discover it who repeat “we know dark matter exists*; we just need to find it” like a religious mantra. This is now ingrained so deeply that it has become difficult to convey even the simple concept that what we call “dark matter” is really just evidence of a discrepancy: we do not know whether it is literally some kind of invisible mass, or a breakdown of the equations that lead us to infer invisible mass.

I try to look at all sides of a problem. I can say nice things about dark matter (and cosmology); I can point out problems with it. I can say nice things about MOND; I can point out problems with it. The more common approach is to presume that any failing of MOND is an automatic win for dark matter. This is a simple-minded logical fallacy: just because MOND gets something wrong doesn’t mean dark matter gets it right. Indeed, my experience has been that cases that don’t make any sense in MOND don’t make any sense in terms of dark matter either. Nevertheless, this attitude persists.

*I made this flowchart as a joke in 2012, but it persists in being an uncomfortably fair depiction of how many people who work on dark matter approach the problem.*

I don’t know what is right, but I’m pretty sure this attitude is wrong. Indeed, it empowers a form of magical thinking: dark matter has to be correct, so any data that appear to contradict it are either wrong, or can be explained with feedback. Indeed, the usual trajectory has been denial first (that can’t be true!) and explanation later (we knew it all along!) This attitude is an existential threat to the scientific method, and I am despondent in part because I worry we are slipping into a post-scientific reality, where even scientists are little more than priests of a cold, dark religion.

*If we’re sure dark matter exists, it is not obvious that we need to be doing expensive experiments to find it.

Why bother?

Bias all the way down

It often happens that data are ambiguous and open to multiple interpretations. The evidence for dark matter is an obvious example. I frequently hear permutations on the statement

We know dark matter exists; we just need to find it.

This is said in all earnestness by serious scientists who clearly believe what they say. They mean it. Unfortunately, meaning something in all seriousness, indeed, believing it with the intensity of religious fervor, does not guarantee that it is so.

The way the statement above is phrased is a dangerous half-truth. What the data show beyond any dispute is that there is a discrepancy between what we observe in extragalactic systems (including cosmology) and the predictions of Newton & Einstein as applied to the visible mass. If we assume that the equations Newton & Einstein taught us are correct, then we inevitably infer the need for invisible mass. That seems like a very reasonable assumption, but it is just that: an assumption. Moreover, it is an assumption that is only tested on the relevant scales by the data that show a discrepancy. One could instead infer that theory fails this test – it does not work to predict observed motions when applied to the observed mass. From this perspective, it could just as legitimately be said that

A more general theory of dynamics must exist; we just need to figure out what it is.

That puts an entirely different complexion on exactly the same problem. The data are the same; they are not to blame. The difference is how we interpret them.

Neither of these statements are correct: they are both half-truths; two sides of the same coin. As such, one risks being wildly misled. If one only hears one, the other gets discounted. That’s pretty much where the field is now, and has it been stuck there for a long time.

That’s certainly where I got my start. I was a firm believer in the standard dark matter interpretation. The evidence was obvious and overwhelming. Not only did there need to be invisible mass, it had to be some new kind of particle, like a WIMP. Almost certainly a WIMP. Any other interpretation (like MACHOs) was obviously stupid, as it violated some strong constraint, like Big Bang Nucleosynthesis (BBN). It had to be non-baryonic cold dark matter. HAD. TO. BE. I was sure of this. We were all sure of this.

What gets us in trouble is not what we don’t know. It’s what we know for sure that just ain’t so.
Josh Billings

I realized in the 1990s that the above reasoning was not airtight. Indeed, it has a gaping hole: we were not even considering modifications of dynamical laws (gravity and inertia). That this was a possibility, even a remote one, came as a profound and deep shock to me. It took me ages of struggle to admit it might be possible, during which I worked hard to save the standard picture. I could not. So it pains me to watch the entire community repeat the same struggle, repeat the same failures, and pretend like it is a success. That last step follows from the zeal of religious conviction: the outcome is predetermined. The answer still HAS TO BE dark matter.

So I asked myself – what if we’re wrong? How could we tell? Once one has accepted that the universe is filled with invisible mass that can’t be detected by any craft available known to us, how can we disabuse ourselves of this notion should it happen to be wrong?

One approach that occurred to me was a test in the power spectrum of the cosmic microwave background. Before any of the peaks had been measured, the only clear difference one expected was a bigger second peak with dark matter, and a smaller one without it for the same absolute density of baryons as set by BBN. I’ve written about the lead up to this prediction before, and won’t repeat it here. Rather, I’ll discuss some of the immediate fall out – some of which I’ve only recently pieced together myself.

The first experiment to provide a test of the prediction for the second peak was Boomerang. The second was Maxima-1. I of course checked the new data when they became available. Maxima-1 showed what I expected. So much so that it barely warranted comment. One is only supposed to write a scientific paper when one has something genuinely new to say. This didn’t rise to that level. It was more like checking a tick box. Besides, lots more data were coming; I couldn’t write a new paper every time someone tacked on an extra data point.

There was one difference. The Maxima-1 data had a somewhat higher normalization. The shape of the power spectrum was consistent with that of Boomerang, but the overall amplitude was a bit higher. The latter mattered not at all to my prediction, which was for the relative amplitude of the first to second peaks.

Systematic errors, especially in the amplitude, were likely in early experiments. That’s like rule one of observing the sky. After examining both data sets and the model expectations, I decided the Maxima-1 amplitude was more likely to be correct, so I asked what offset was necessary to reconcile the two. About 14% in temperature. This was, to me, no big deal – it was not relevant to my prediction, and it is exactly the sort of thing one expects to happen in the early days of a new kind of observation. It did seem worth remarking on, if not writing a full blown paper about, so I put it in a conference presentation (McGaugh 2000), which was published in a journal (IJMPA, 16, 1031) as part of the conference proceedings. This correctly anticipated the subsequent recalibration of Boomerang.

The figure from McGaugh (2000) is below. Basically, I said “gee, looks like the Boomerang calibration needs to be adjusted upwards a bit.” This has been done in the figure. The amplitude of the second peak remained consistent with the prediction for a universe devoid of dark matter. In fact, if got better (see Table 4 of McGaugh 2004).

Plot from McGaugh (2000): The predictions of LCDM (left) and no-CDM (right) compared to Maxima-1 data (open points) and Boomerang data (filled points, corrected in normalization). The LCDM model shown is the most favorable prediction that could be made prior to observation of the first two peaks; other then-viable choices of cosmic parameters predicted a higher second peak. The no-CDM got the relative amplitude right a priori, and remains consistent with subsequent data from WMAP and Planck.

This much was trivial. There was nothing new to see, at least as far as the test I had proposed was concerned. New data were pouring in, but there wasn’t really anything worth commenting on until WMAP data appeared several years later, which persisted in corroborating the peak ratio prediction. By this time, the cosmological community had decided that despite persistent corroborations, my prediction was wrong.

That’s right. I got it right, but then right turned into wrong according to the scuttlebutt of cosmic gossip. This was a falsehood, but it took root, and seems to have become one of the things that cosmologists know for sure that just ain’t so.

How did this come to pass? I don’t know. People never asked me. My first inkling was 2003, when it came up in a chance conversation with Marv Leventhal (then chair of Maryland Astronomy), who opined “too bad the data changed on you.” This shocked me. Nothing relevant in the data had changed, yet here was someone asserting that it had like it was common knowledge. Which I suppose it was by then, just not to me.

Over the years, I’ve had the occasional weird conversation on the subject. In retrospect, I think the weirdness stemmed from a divergence of assumed knowledge. They knew I was right then wrong. I knew the second peak prediction had come true and remained true in all subsequent data, but the third peak was a different matter. So there were many opportunities for confusion. In retrospect, I think many of these people were laboring under the mistaken impression that I had been wrong about the second peak.

I now suspect this started with the discrepancy between the calibration of Boomerang and Maxima-1. People seemed to be aware that my prediction was consistent with the Boomerang data. Then they seem to have confused the prediction with those data. So when the data changed – i.e., Maxima-1 was somewhat different in amplitude, then it must follow that the prediction now failed.

This is wrong on many levels. The prediction is independent of the data that test it. It is incredibly sloppy thinking to confuse the two. More importantly, the prediction, as phrased, was not sensitive to this aspect of the data. If one had bothered to measure the ratio in the Maxima-1 data, one would have found a number consistent with the no-CDM prediction. This should be obvious from casual inspection of the figure above. Apparently no one bothered to check. They didn’t even bother to understand the prediction.

Understanding a prediction before dismissing it is not a hard ask. Unless, of course, you already know the answer. Then laziness is not only justified, but the preferred course of action. This sloppy thinking compounds a number of well known cognitive biases (anchoring bias, belief bias, confirmation bias, to name a few).

I mistakenly assumed that other people were seeing the same thing in the data that I saw. It was pretty obvious, after all. (Again, see the figure above.) It did not occur to me back then that other scientists would fail to see the obvious. I fully expected them to complain and try and wriggle out of it, but I could not imagine such complete reality denial.

The reality denial was twofold: clearly, people were looking for any excuse to ignore anything associated with MOND, however indirectly. But they also had no clear prior for LCDM, which I did establish as a point of comparison. A theory is only as good as its prior, and all LCDM models made before these CMB data showed the same thing: a bigger second peak than was observed. This can be fudged: there are ample free parameters, so it can be made to fit; one just had to violate BBN (as it was then known) by three or four sigma.

In retrospect, I think the very first time I had this alternate-reality conversation was at a conference at the University of Chicago in 2001. Andrey Kravtsov had just joined the faculty there, and organized a conference to get things going. He had done some early work on the cusp-core problem, which was still very much a debated thing at the time. So he asked me to come address that topic. I remember being on the plane – a short ride from Cleveland – when I looked at the program. Nearly did a spit take when I saw that I was to give the first talk. There wasn’t a lot of time to organize my transparencies (we still used overhead projectors in those days) but I’d given the talk many times before, so it was enough.

I only talked about the rotation curves of low surface brightness galaxies in the context of the cusp-core problem. That was the mandate. I didn’t talk about MOND or the CMB. There’s only so much you can address in a half hour talk. [This is a recurring problem. No matter what I say, there always seems to be someone who asks “why didn’t you address X?” where X is usually that person’s pet topic. Usually I could do so, but not in the time allotted.]

About halfway through this talk on the cusp-core problem, I guess it became clear that I wasn’t going to talk about things that I hadn’t been asked to talk about, and I was interrupted by Mike Turner, who did want to talk about the CMB. Or rather, extract a confession from me that I had been wrong about it. I forget how he phrased it exactly, but it was the academic equivalent of “Have you stopped beating your wife lately?” Say yes, and you admit to having done so in the past. Say no, and you’re still doing it. What I do clearly remember was him prefacing it with “As a test of your intellectual honesty” as he interrupted to ask a dishonest and intentionally misleading question that was completely off-topic.

Of course, the pretext for his attack question was the Maxima-1 result. He phrased it in a way that I had to agree that those disproved my prediction, or be branded a liar. Now, at the time, there were rumors swirling that the experiment – some of the people who worked on it were there – had detected the third peak, so I thought that was what he was alluding to. Those data had not yet been published and I certainly had not seen them, so I could hardly answer that question. Instead, I answered the “intellectual honesty” affront by pointing to a case where I had said I was wrong. At one point, I thought low surface brightness galaxies might explain the faint blue galaxy problem. On closer examination, it became clear that they could not provide a complete explanation, so I said so. Intellectual honesty is really important to me, and should be to all scientists. I have no problem admitting when I’m wrong. But I do have a problem with demands to admit that I’m wrong when I’m not.

To me, it was obvious that the Maxima-1 data were consistent with the second peak. The plot above was already published by then. So it never occurred to me that he thought the Maxima-1 data were in conflict with what I had predicted – it was already known that it was not. Only to him, it was already known that it was. Or so I gather – I have no way to know what others were thinking. But it appears that this was the juncture in which the field suffered a psychotic break. We are not operating on the same set of basic facts. There has been a divergence in personal realities ever since.

Arthur Kosowsky gave the summary talk at the end of the conference. He told me that he wanted to address the elephant in the room: MOND. I did not think the assembled crowd of luminary cosmologists were mature enough for that, so advised against going there. He did, and was incredibly careful in what he said: empirical, factual, posing questions rather than making assertions. Why does MOND work as well as it does?

The room dissolved into chaotic shouting. Every participant was vying to say something wrong more loudly than the person next to him. (Yes, everyone shouting was male.) Joel Primack managed to say something loudly enough for it to stick with me, asserting that gravitational lensing contradicted MOND in a way that I had already shown it did not. It was just one of dozens of superficial falsehoods that people take for granted to be true if they align with one’s confirmation bias.

The uproar settled down, the conference was over, and we started to disperse. I wanted to offer Arthur my condolences, having been in that position many times. Anatoly Klypin was still giving it to him, keeping up a steady stream of invective as everyone else moved on. I couldn’t get a word in edgewise, and had a plane home to catch. So when I briefly caught Arthur’s eye, I just said “told you” and moved on. Anatoly paused briefly, apparently fathoming that his behavior, like that of the assembled crowd, was entirely predictable. Then the moment of awkward self-awareness passed, and he resumed haranguing Arthur.

Triton Station

A Blog About the Science and Sociology of Cosmology and Dark Matter

Category: Personal Experience