Tuesday, June 18, 2019

Brace for the oncoming deluge of dark matter detectors that won’t detect anything

Imagine an unknown disease spreads, causing temporarily blindness. Most patients recover after a few weeks, but some never regain eyesight. Scientists rush to identify the cause. They guess the pathogen’s shape and, based on this, develop test-stripes and antigens. If one guess doesn’t work, they’ll move on to the next.

Doesn’t quite sound right? Of course it does not. Trying to identifying pathogens by guesswork is sheer insanity. The number of possible shapes is infinite. The guesses will almost certainly be wrong. No funding agency would pour money into this.

Except they do. Not for pathogen identification, but for dark matter searches.

In the past decades, the searches for the most popular dark matter particles have failed. Neither WIMPs nor axions have shown up in any detector, of which there have been dozens. Physicists have finally understood this is not a promising method. Unfortunately, they have not come up with anything better.

Instead, their strategy is now to fund any proposed experiment that could plausibly be said to maybe detect something that could potentially be a hypothetical dark matter particle. And since there are infinitely many such hypothetical particles, we are now well on the way to building infinitely many detectors. DNA, carbon nanotubes, diamonds, old rocks, atomic clocks, superfluid helium, qubits, Aharonov-Bohm, cold atom gases, you name it. Let us call it the equal opportunity approach to dark matter search.

As it should be, everyone benefits from the equal opportunity approach. Theorists invent new particles (papers will be written). Experimentalists use those invented particles as motivation to propose experiments (more papers will be written). With a little luck they get funding and do the experiment (even more papers). Eventually, experiments conclude they didn’t find anything (papers, papers, papers!).

In the end we will have a lot of papers and still won’t know what dark matter is. And this, we will be told, is how science is supposed to work.

Let me be clear that I am not strongly opposed to such medium scale experiments, because they typically cost “merely” a few million dollars. A few millions here and there don’t put overall progress at risk. Not like, say, building a next larger collider would.

So why not live and let live, you may say. Let these physicists have some fun with their invented particles and their experiments that don’t find them. What’s wrong with that?

What’s wrong with that (besides the fact that a million dollars is still a million dollars) is that it will almost certainly lead nowhere. I don’t want to wait another 40 years for physicists to realize that falsifiability alone is not sufficient to make a hypothesis promising.

My disease analogy, as any analogy, has its shortcomings of course. You cannot draw blood from a galaxy and put it under a microscope. But metaphorically speaking, that’s what physicists should do. We have patients out there: All those galaxies and clusters which are behaving in funny ways. Study those until you have good reason to think you know what’s the pathogen. Then, build your detector.

Not all types of dark matter particles do an equally good job to explain structure formation and the behavior of galaxies and all the other data we have. And particle dark matter is not the only explanation for the observations. Right now, the community makes no systematic effort to identify the best model to fit the existing data. And, needless to say, that data could be better, both in terms of sky coverage and resolution.

The equal opportunity approach relies on guessing a highly specific explanation and then setting out to test it. This way, null-results are a near certainty. A more promising method is to start with highly non-specific explanations and zero in on the details.

The failures of the past decades demonstrate that physicists must think more carefully before commissioning experiments to search for hypothetical particles. They still haven’t learned the lesson.

56 comments:

  1. Good point. It is only fair that the dark-matter search receives the same criticism as nextgen-LHC, if there is one (and it seems that there definitely is). I don't see any reason why a not-so-promising science should be funded, even if it is relatively cheap.

    One plausible reason (not a very good one) could be that this is the best we can do, but seemingly it is not the case. Or maybe scientists have exhausted their ideas in theory development suitable to describe the existing data?

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  2. Maybe a good thing would be for the scientific community to sit down and agree on when and under which circumstances the particle dark matter hypothesis is definitely falsified by the numerous failed attempts at its direct detection. I'm confident given both the astrophysical and earth based labs observations that it should be possible to constraint it such as it is definitely ruled out once all the reasonable exploratory paths have been tested to no avail.

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  3. You mean that doctors don't try to identify pathogens by guesswork? Of course they do. The alternative would be looking carefully at all the symptoms of the disease, and deducing the pathogen from that, and that's patently insane. Luckily, a pathogen will probably be a virus, a bacterium, a fungus, or a protozoan. And if it's something else, you might just get a Nobel prize for figuring that out.

    And for dark matter, while there are lots more possibilities than there are for pathogens, there are clearly not infinitely many, and your chances of guessing right are more than zero. These are perfectly reasonable experiments, even if they probably won't find anything.

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    1. Note that I carefully wrote the pathogen's shape, not the pathogen.

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    2. "there are clearly not infinitely many"

      There are infinitely many extensions of the standard model that fit the bill. If you can prove that this isn't so, this would be the most remarkable breakthrough in dark matter research ever.

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  4. One of my favorite websites to go to for all things related to Dark Matter/Energy is Stacey McGaugh's Triton Station. It's a smorgasbord of information on the issues surrounding this cosmological mystery. Just the other day I came across a nugget of information that I wasn't aware of previously. In the comment section of one of his posts he points out that the acceleration regime that the Pioneer spacecraft are subject to in the Sun's gravity field is still 4 orders of magnitude above Milgrom's acceleration scale of A0, and these craft would need to reach a distance of 1/10th light year from the sun before the solar field matches A0. Am going from memmory, but I'll see if I can find the original statement over at his website.

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  5. What is your guess: dark matter is not a "particle" which these experiments could detect (e.g. primordial black holes, macroscopic (hence self-interacting) dark matter, superfluid dark matter), something like MOND is right, some combination, or something else entirely?

    There have been a few famous bets in the history of physics. Why not try to find someone who will pay you, say, 10,000 if no such experiment detects dark matter within, say, 10 years?

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    1. As I have said already many times before, I place bets by choosing research topics. But this is beside the point. I cannot as one person replace the work of a whole community. This community needs to think about what data is most likely to decrease the underdetermination of the models. Randomly financing super-specialized measurements here and there is almost certainly not going to help.

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  6. Well, I would understand your point of we had an alternative, but as of now we're stuck. A lot of people are already working on theory, a lot of people are already working on galaxies and astrophysics, and, as a result, a lot of models are already out there. The experimental effort has already shown that there is probably no way that WIMPs are real, which I would say is quite a valuable information.

    Also, besides the lack of alternative in dark matter investigation, there's also a lack of alternatives in particle physics altogether: the only fields that have still something to say involve astroparticle physics, in my opinion. The experiments in this field are already pushing multiple technologies (bubble chambers, TPC with liquid noble gases, solid state experiments, cryogenic experiments, proportional counters...) and they cost a tiny fraction of the whole budget of particle physics. The same detectors/technologies used for dark matter search can also be used to investigate in more detail neutrino physics and we definitely know that neutrinos are weirdos.

    So, I have a question with you: what should be in your view a good alternative? Sitting back and wait till someone has a breakthrough? Give money to other experiments (which kind)?

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    1. Ospizio,

      I explained in my blogpost what the community should do, but evidently that wasn't clear enough, so here is another attempt.

      We have a lot of data with evidence for dark matter or whatever else it is. This data needs to be analyzed in a model-independent way. It makes no sense that everyone and their dog invents some highly specific particle and then try to see if they can make it fit the data. We know the answer to this: If you make enough effort you can make anything fit the data. There is nothing to be learned from this. People do it simply because that's what they have been taught to do. It doesn't work. It needs to stop.

      The data have told us for decades that the simplest pressureless fluid dark matter models are hard to fit to galaxies. That's the whole modified gravity, Tully-Fisher debate. Now, look, you may not like modified gravity (and I understand that), but forget this for a moment. The mere existence of this debate tells you is that just parameterically, a pressurless fluid is *not* overall the best fit to the data. Instead, the best fit is a pressureless fluid in some cases, and something else in other cases. Which cases? What something else? No one knows.

      Why not? Well for starters because no one ever analyzes the data. To be fair, it's also not an easy analysis and 10 years ago it may not even have been possible because of lack of computing power. But it's possible now.

      The answer would tell us something about the (likely) self-interaction of the stuff and its (likely) interactions with baryons. Which is information that you can reformulate in ways of a modified gravity approach (shielding distance or whatever). I am quite agnostic on the matter (I feel like if you can formulate the math either which way it's the same thing).

      How much you learn from this depends of course on how good your data is. And the data could be better. Eg, directional dependence is hugely valuable but hard to come by. So are redshift measurements because you need those to determine the age of a galaxy. You need sky coverage to get good statistics for weaker effects. And so on. (Better ask an astrophysicist.)

      Most importantly, this is not an analysis anyone can do with a pencil on paper and with one grad student. It's a computationally hard problem that requires both funding and people power and it's not getting done because too many people are in love with their personal little dark matter model.

      And to reiterate what I already said, once you have pinned down what it most likely interacts with and by what strength, you can think about what detector to build.

      Concretely, just to name an example. It may well turn out the stuff doesn't couple to Fmunu (with high probability), which would make 50% of the planned experiments immediately redundant.

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    2. Here Sabine is specifically calling for research! Something that will need funding to get done!

      Such an attempt to have a large collaboration working to systematically analyze the data will employ many many dark matter researchers and computer scientists and astrophysicists.

      Don't let it be said that Sabine does not give positive direction and only negative criticism.

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  7. I guess that only a déluge of detectors focusing on the Constellation of Taurus might be successfull.

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  8. What about the hypothesis that dark matter is made of particles of negative mass repelling ordinary matter, and therefore living in the voids in between galaxies? Do you consider it a viable hypothesis?

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  9. Sabine, a nice post as always. I wonder if there are any proposals for trying to measure MOND effects? Some ideas here,
    https://en.wikipedia.org/wiki/Modified_Newtonian_dynamics#Proposals_for_testing_MOND

    And I enjoyed this paper.
    https://arxiv.org/pdf/astro-ph/0602266.pdf

    Sending probes out to the small and fast moving saddle points would be a challenge, I wonder if there are any people thinking about it?

    And finally how about launching a 'huge' corner cube reflector out to ~0.1 light year from Earth and track how it moves. (Yeah that's a challenge too.)

    George

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  10. If there is nothing to detect and it doesn't detect anything that would be a good thing. But what if there's a project that's too big to fail and they just generate some data that looks exactly like a preliminary simulation of what they were hoping to detect?

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  11. Honest question - does the detection of gravitational waves, and the investment in further improvements in this area, provide a new source of data potentially valuable in developing and testing hypotheses about the nature of dark matter? Or not so much?

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    1. Rollo,

      Needless to say, there are also people who have proposed to use gravitational wave interferometers to test some types of dark matter. See eg this recent paper.

      Now, look, my point is that all these supposed tests are for highly specific particles that have been invented basically because you can test them in a way that someone happened to be working on. It is not a promising approach.

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  12. Feynman himself said in one of his lectures that you start by guessing.

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    1. And, uuuh, the master has spoken, preach his word! Seriously, what kind of argument is this supposed to be? How about using your own brain?

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    2. Feynman said that when you start with trying to guess what the natural law is, you should calculate the consequences of your guess and carefully check how everything else that is known would fit into it, and make sure it explains more than just the presumptions you started from

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  13. I did a back of the envelope calculation on how gravity as 2-space plus time on a stretched horizon has edge states similar to topological insulators. This can I think get “caught” in one dimension larger, much in the same way supercooled water can exist. This would mean there is a form of gravitation that has a gravitational potential one gets in 2 spatial dimensions

    Φ = -∫F/m·dr = \sqrt{GMa} ln(r/GM).

    with 1/a = √{Λ/3}. In effect the rapid collapse of the inflationary vacuum with reheating is such that holographic states on the horizon in effect maintain their 2-dim form. So maybe there is a field effect aspect to gravitation due to physics of the very early universe.

    It might be that this is how this strange from of gravity emerges. This might even have measurable consequences. Gauss' law ∫F·dA = 4πGρ means the density in the gravitation source increases with radius ρ = ρ_0r. This source of gravitation is most likely the vacuum, which means potentially there are subtle quantum spectral effects with atoms, such as small differences in spectra between atoms nearer the center of the galaxy and those towards the exterior.

    The search for dark matter has not been all that badly done. The idea it is some weak interaction particle is a fair hypothesis. Some people proposed neutrinos that have very small kinetic, the neutralino (a condensate of superpartners) was fair, the axion is still some possibility. The weakly interacting particle appears headed out the door. The LUX-ZEPLIN III, I think it is called, is the last chance for WIMPS. As it proceeds it appears to be following the dictum of Sherlock Holmes, which is to examine the most probable cause and if that is eliminated you go to the next and so on. The search for dark matter as some particle that makes a detector click has maybe another 10 years to go. WIMPS may get eliminated this year or next. At some point if a decent particle candidate does not make a detector click enough to reach 5 sigma then other ways of thinking about this may be given more serious attention.

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  14. Perhaps the dark matter question is one of personal style. Particle science is reductionist by its nature. Maybe the final solution to the dark matter dilemma is actually a holistic one. Dark matter could be comprised of one or more ordinary particles in combination such that when placed under special conditions behave in unexpected ways. Possibly, these special conditions are not usually found here on earth or at least not recognized as unique or meaningful but happen all the time in space. How would a gatekeeper in particle physics handle such an incompatible conceptual conundrum which is completely contrary to that persons training and proclivities?

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  15. Maybe instead of continuing their futile search for a dark matter life preserver for their inadequate gravitational models based on formalisms derived in the context the solar system, theorists might try deriving new formalisms appropriate to the physical systems they are actually trying to model.

    Coming up with a good way to accurately model the self-gravitation of galactic disks would be a good place to start.

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  16. I suppose squeezing in dark matter to explain the missing gravitational forces/mass in the universe isn't working. Other theories may better solve the enigma. More monies spent exploring the electromagnetic interactions of plasma in the universe may seem on the fringe, but research with Tokomak reactors and compressed plasma appear to be a successful leading edge in finding answers.
    I'm not a physicist, but see dead ends in dark matter research and String theory.

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    1. (IanaP) I always thought postulating dark matter was odd. If GR doesn't work for galaxies, maybe the problem is with GR? After all, galactic structures weren't even know to exist when Einstein was working on GR. Surely we can't expect someone to come up with a theory that's valid at all times and places when the data available is so limited. It's hubris not to expect surprises in observing distant parts of the universe.

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    2. Exactly! Complex systems will exhibit "emergent properties" that can't be reduced/explained by the properties of its elementary components, and obviously galaxies are very complex systems. But many physicists are unable to free themselves from the narrow reductionist mindset and will forever try to find ghost dark matter particles, they really have not internalized that the axiomatic method at the root of fundamental physics is intrinsically flawed.

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    3. "Complex systems will exhibit "emergent properties",,,"

      Maybe they will, maybe they won't; I'm agnostic about emergent properties. My point was simply that it's hubris to suppose that anyone working on Earth c. 1915 could have discovered a theory of gravity that would be valid at all times and places. GR is beautiful, but as Sabine has reiterated, that's no guarantee of truth.

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  17. Dear Dr Hossenfelder,

    Peter is right.

    > We have patients out there: All those galaxies
    > and clusters which are behaving in funny ways.
    > Study those until you have good reason to think you know what’s the pathogen.

    This is correct: the galaxies are the patients. But it would be
    patently absurd to wait with the drawing of blood until one has
    has good clues, derived only from their symptoms, about the pathogen.

    > You cannot draw blood from a galaxy and put it under a microscope.

    You can! We are in the middle of the body of one patient: our
    Galaxy. The microscope is the dark matter detector.
    You can't see each pathogen with
    all types of microscopes and you can't see each dark matter
    candidate with all types of DM detectors.
    Therefore, like a myriad of different types
    of microscopes is employed in the
    search for pathogens, a myriad of qualitatively
    different detectors needs to be employed in the search for
    dark matter. And we experimentalists do not
    only look for pathogens (or even only "shapes of pathogens") that have been suggested by you theorists,
    we experimentalists look for any anomaly, like Pasteur did.

    > But metaphorically speaking, that’s what physicists should do.

    Metaphorically this advice means: search for dark matter.

    Franziska

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    1. You missed the point. A microscope would show you all that there is the blood. A dark matter detector tuned to find a specific particle with a specific interaction and a specific mass and more specific properties like specific excitations on specific condensates and specific mixings with specific other particles will not do that.

      Yes, sure, you look for anomalies. And you know what, you will find them.

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    2. > A microscope would show you all there is in the blood.

      No, there is no and there will never be a microscope "which shows all possible pathogens".

      E.g. there is unfortunately no microscope available that
      shows cancer cells from a metastizing tumor in the human blood.
      There are special fluorescence microscopes with which
      such cells can be seen in the blood of rats, but
      for humans it is still a research topic.

      > A dark matter detector tuned to find a specific particle ...
      > will not do that.

      Yes, indeed, there will never be a "dark matter detector which
      shows all possible dark matter particles".
      That's why we need the wide variety of them that you criticised
      so scathingly.

      > And the data could be better. Eg, directional dependence is
      > hugely valuable but hard to come by. So are redshift measurements
      > because you need those to determine the age of a galaxy.

      Is this your advice to us experimentalists working on direct
      dark matter detection? Stop your experiments and start to compete
      with competent colleagues like your friend Stacy
      McGaugh (who are already doing this for decades)
      to make red-shift measurements on galaxies?

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    3. A cancer cell is not a pathogen.

      In any case, I don't see the point in going on about this because my analogy clearly was not meant seriously.

      No, I am not talking to you experimentalists at all, because that would be wasting my time. I am talking to the people who give you money. Because they should stop doing that.

      Delete
    4. > A cancer cell is not a pathogen.

      In the bloodstream cancer cells cause mestases which eventually
      kill the patient. So within your metaphor
      one would definitely like to be able to see them
      no matter how "pathogen" is correctly defined.

      > No, I am not talking to you experimentalists at all,
      > because that would be wasting my time.

      A theorist wastes her time when she talks to experimentalists
      in general?

      > I am talking to the people who give you money. Because they should stop doing that.

      OK, so your advice is: "Fire all physicists working on direct
      dark matter detection."

      Delete
    5. "A theorist wastes her time when she talks to experimentalists in general?"

      I'm not a theorist, I'm a phenomenologist. I have organized a conference series whose purposes is to get theorists and experimentalists to talk to each other, so the answer to your question is demonstrably no, I am talking about a disease of certain communities, communities which have become overly convinced of their own relevance despite a decades lasting lack of progress.

      "OK, so your advice is: "Fire all physicists working on direct dark matter detection."

      No, that does not make sense because they are intelligent and well educated people from whom science has much to benefit. (Or most of them, anyway.) Letting them go would be a waste of resources. They should however be strongly encouraged to think about how to make progress. Building detectors to test models that amount to little more than guesswork is not a promising method. I have explained why but unfortunately, by my personal experience, experimentalists have a hard time understanding that the philosophy of science matters and that hypothesis selection is something they should pay attention to.

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    6. I can see there is some confusion over what cancer is. Cancer is just a breakdown in the molecular machinery. There are a number of pathways to cancer. They all in general share some fairly common features. One process can be a gene mutation, called a single nucleotide polymorphsm, in a gene within a somatic cell that expresses a tyrosine receptor that is flawed. These are activated by phosphorylation of a tyrosine residue which changes the shape of the molecule. In doing so this activates a set of pathways with protein dependent kinases that changes the cell from the S phase of the cell cycle and initiates cell division. This flawed receptor, which usually is activated by some co-enzyme or “G-factor.” will start to auto-phosphorylate. This then leads to runaway cell growth. The polycyclic aromatic hydrocarbons in smoke often bind onto the p-53 gene, which may then induce a nucleotide to change its purine or pyrimidine.

      However, there must be more. If it were just this these cells would die. The retinoblastoma genes would kick in and lead to apoptosis or programmed cell death. If that is knocked out then these cells will use up their telemere ends, where replicase binds onto and shortens each time, and these cells would stop dividing. So other cell signaling pathways have to be disordered to permit the somatic cell to express telomerase that replenishes telemere ends. Stem and germ cell lines have this, and is one reason leukemia and lymphoma happens. For a somatic cell if a certain set of genes are changed and these cell signaling processes fail to catch the aberrant cell line then cancer can take place. For tissue cancers it is also necessary for the cells to start producing cytokines that signal the growth of capillaries into the cancer cells. That permits a small cluster to become a tumor.

      The separation of cancer cells from pathogens is not that strong. Some cancers are due to viral DNA, such as the Sarc gene from a foreign animal, usually chickens, that is encorporated into a virion which then after a human is infected gets incorporated into the DNA of somatic cells. The Sarc gene is a cell cycle regulator gene that in a human somatic cell causes all sorts of havoc. This gene hopping means that in one sense this cancer could be seen as a pathogen.

      My undergraduate department had specializations, and I did biophysics. A lot of that stuff is pretty rusty these days, but I do recall some of it. I have even cloned genes and the like.

      Delete
  18. Hi SABINE !!!
    and friends.

    Well, what have we here ?
    I don't know what to make of it
    at the moment.
    Perhaps discussing discussion.
    Theorising on theories,
    Commenting on comments.
    Really, ?
    Personally, I've just gone through Asymtotic Safety,
    Quantum Loop Gravity, and
    I'm almost done with
    Causal Dynamical Triangulation. and..
    Don't think, for a moment, I don't realize that CDT is a direct branch of Feynman's
    ' sum over histories' notion of
    Quantum theory/mechanics.
    That's not my point.
    -(I appreciate Sabine's remark
    about 'the master has spoken'.
    but in regards to Feynman, Gell-Mann, Einstein,
    or a homeless person
    on the street.
    I respect them all.
    I don't have to agree with
    or even like them.)
    (- or even know them)

    What I'm trying to say is
    that,
    If your 'knowledge' is -
    A theory - based on a theory.
    Based on a theory that's
    based on a theory.
    - if you climb up on the roof
    and look down.
    ... you realize,
    it's a house of cards.

    If the foundations
    of what we 'know'
    are of an assumptive
    or presumptive nature,

    There is no doubt, my friends,
    we've taken a precarious step
    away from Science.

    Love Your Work.

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  19. "Dark Matter" has something to do with (a new) quantum spacetime theory, mirror matter, or ... panpsychism - dark matter is matter that is shy :).

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  20. A 2016 study found that the total gravity present within galaxies is directly proportional to the amount of gravity provided by the visible matter. This fact argues against the existence of dark matter, since the number of invisible particles should be independent of the number of visible particles. It seems to me that a rational person wouldn't expect to see all of the matter in the universe. The universe is enormous and most of it's matter, though baryonic, isn't part of any light-producing structure such as a star or is beyond the reach of our telescopes. Yet, even the black holes and diffuse matter that hasn't yet coalesced into something we can see are nonetheless exerting a gravitational force on the matter that we can see.

    Sabine, I don't share your extensive knowledge of the subject. Could you please explain why the people arguing for the existence of dark matter aren't crazy.

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    1. Because galactic rotation curves are only one of several types of data that speak for dark matter, also the study that you mention didn't include all types of galaxies.

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  21. Hi Sabine,

    Your analogy seems to be saying that each of the dark matter detectors proposed will detect exactly one kind of the infinitely many possible kinds of dark matter that there might be, and thus each of them has a chance of 1/∞ of working, so we might as well not bother.

    This is misleading ... all of them will detect dark matter from many of the infinite possible theories of physics, so some of them might actually have a reasonable chance of working, and thus be worth funding. But of course, the people funding the experiments need to evaluate the proposed experiments carefully. Some of the proposals are undoubtedly not worth funding.

    It's also quite possible that dark matter is undetectable with any conceivable practical technology ... for example, it could be made of heavy sterile neutrinos that only interact with other neutrinos. But even in this case, isn't it worth ruling some of the other types of dark matter out, provided we can do it relatively inexpensively?

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    1. Peter,

      Well, what is it, they have a reasonable chance of working or quite possibly dark matter maybe undetectable? Why not think a little more about why you believe the chance is "reasonable". What makes you think so? Is this a belief or is it based on evidence?

      Delete
  22. Yes, the situation about dark matter is depressing. There are no indications of a solution in the public discussion. But what also depresses me is the missing open-mindedness of official physics. Example: there was the detection of two galaxies which have very little light and very little dark matter. Can we learn something from this observation? I asked this question a keynote speaker of dark matter at a physics conference. His answer was: do not believe everything what you read in the newspapers.
    Is this a good way to react on new (and unexpected) data? And are we ourselves sufficiently open-minded?

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    1. I have seen other results about dark matter being less abundant in low luminosity galaxies, I am not saying this is always the case and we obviously don't understand the mechanisms behind this, but here is a thought: what if the photon does have a mass? Due to some Lorentz invariance issue we don't quite understand, it still travels at the speed of light? JP Vigier in a 1997 paper suggested a lower limit mass for the photon of 10^-68 Kg based on an uncertainty relationship.

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  23. Experimental physics and unexpected discoveries often proceed in chaotic non-textbook ways without any proper theoretical motivation. But it takes decades to develop the technologies needed to make a particular subclass of experiments reach the sensitivity or precision that theoreticians might find interesting. This is necessarily a very inefficient processs, but some part of basic science has always been like that, so I ask you to keep an open mind.

    I've seen that you value highly the muon g-2 experiment, for a long part of its history in the 20th century, the motivation for measuring particle properties to extremely high precision was highly questioned (e.g., "what are you, a metrologist?" "Just because something can be measured to high precision does not mean it should be measured", "Precision for precision's own sake is ridiculous"), since new discoveries were made in colliders. I personally remember a time when gravity wave detection was considered fringe science ("what is that guy spending 20 years mechanically stabilizing his mirror, he is orders of magnitude away from any interesting level where anything could possibly be detected").

    "It is too much a shot in the dark" "They are playing with taxpayer money" "They are messing with the futures of PhD students" All this has been said before, and you are right that in many cases it turns out to be the case, but in a small percentage of cases there is extreme payoff.

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  24. I remember my first physics department symposium in the mid 80s where the guest speaker presented a model of how WIMPs inside the sun could interact in certain ways with neutrinos to alter the flavors we were seeing in dark matter experiments on Earth. Everybody then was puzzled by the lack of neutrinos that we knew should exist from the nuclear synthesis in the sun, we now know from the 1998 super komiokande results that the neutrinos flavors oscillate on their way to Earth, but back then (as still today) the idea was that dark matter was responsible for things we don't understand. If it takes 30 years to figure out each of our enigmas, not from lack of a larger accelerator but just from lack of decent theoretical models and careful observation, I think we should scale back funding on dark matter projects to induce alternate ideas to come forward.

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  25. Reading the 2nd comment by "ohwilleke" on Stacey McGaugh's "Astronomical Acceleration Scales" post, I was intrigued by his reference to the work of Alexandre Deur, of the University of Virginia. Deur evidently is postulating that graviton-graviton interactions could eliminate the need for Dark Matter made up of some exotic particles. One thing that fascinated me in Deur's 6 May 2009 paper on the arXiv "Implications of Graviton-Graviton Interaction to Dark Matter" (0901.4005), is that it is possible to understand the precession of the perihelion of the planet Mercury from a particle physics perspective. At least, that's how I interpreted what he's saying in the second paragraph of his paper. Have just started reading it, and like all professional papers, will just have to skim over the heavy math parts.

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  26. The large percentage of dark matter in the cosmos being five times more prevalent in mass than ordinary matter implies a number of attributes that dark matter must have. First, since dark matter responds to the force of gravity and therefore subject to gravitational consolidation, it should be a major constituent component of every star, black hole, planet, moon, asteroid, meteor, and dust cloud. Since only ordinary forms of matter are found to be a constituent of everything, dark matter must be ordinary matter/energy that is oftentimes subjected to a reversible transformation that amplifies its gravitational potential by a large factor. Most likely this transformation process is probably both electromagnetic and quantum mechanical in nature. Some process transforms ordinary matter dark to EMF interaction. The dark photon/monopole posits that is hot right now and under test at CERN is more right than wrong. But because of its rarity on earth, the prospects of detecting this special transformative configuration of such ordinary stuff is problematic here on earth because the conditions for its formation are inherently complicated and counterintuitive. Or it simply might be that people have not decided to look at such a case. The search for the unusual transformative interactions that lead to the formation of dark matter being a special state of ordinary matter is more a province of condensed matter physics than particle physics.

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    1. Dark matter does not interact by the electromagnetic field. The EM field dissipates a lot of energy, so matter in gravitational systems may also have what amounts to "friction" which causes orbits and motion to stop. This is how matter in a vortex of gas will clump to form stars. If dark matter does not interact by the EM field it will then not clump.

      Dark matter does exist in halos, which in some ways are clumps. There are a range of ideas about this, where maybe there is a "dark electromagnetism." There may be some additional gauge field, maybe a U(1) field similar to QED, but that is much weaker.

      All particles are really just localizations of quantum numbers. With so called Cheshire cat experiments they can localize in different places. So all there is in the universe with particles are quantum numbers, charges or topological indices. Dark matter if it is composed of particles should then have some set of quantum numbers.

      On the other hand maybe dark matter is some curious aspect of gravitation where edge states of the gravity field manifest themselves in one dimension larger. This edge might be the horizon scale during inflation or in the pocket world perspective the edge where the pocket interfaces with the inflationary spacetime. There may be other ways of thinking about this.

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    2. axions do interact with electromagnetic fields

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    3. Oh yeah, I was not thinking about that! The axion has a Klein-Gordon equation with an EM inhomogenous term such as

      (□+ m^2) φ = -gE·B

      Which has the solution for a stationary phase Ã(x,t) = Ã(x)e^{-iωt} has an approximate solution

      φ(x,t) ≈ φ_0exp(-i√{k^2 - m^2})e^{-iωt} + e^{-i√(gE·B/φ_0)t}

      I think that is ok as a back of envelope calculation. One would really need to work this out coupled with the Maxwell equations.

      There are a couple of things we can observe. The term E·B must mean this occurs in a region that is either not source free or where there is some background field. This for most practical purposes would be a magnetic field. In this way the axion can couple with an electromagnetic wave in a region with an ambient magnetic field so that E·B ≠ 0. So it is reasonable to look for photons with a state given by this interaction. On Earth a very large magnetic field might suffice. If one wants to look at astrophysics then neutron stars might work. This is of course if you can study one that is not “clouded up” with accretion disk and nebular material.

      Looking at astrophysics is the most likely option. The reason is the g coupling term is the S dual of the QCD coupling and is extremely small. The axion from the basic Peccei-Quinn theory removes CP violations from QCD, and this means there is an F_{μν}*F^{μν} “edge state” term. This means the axion is extremely weakly coupled to the QED field. One better look at neutron stars with their enormous 10^9T magnetic fields if one stand much chance of getting any physics out of this. I then would mean that for axion “frozen” in place from inflation would couple to the magnetic field of this galaxy extremely weakly.

      What would this signature from neutron star magnetic fields look like? I am not sure, but I think given that axions are thought to be in a “frozen state” and thus all in almost a fermion condensate that the photons produced would be similar to laser coherent states. Think Einstein's coefficients.

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  27. I totally agree Sabine. My opinion is that given we do not understand enough about gravity yet to say whether, Dark Matter is a thing or not, I think the chase to find Dark Matter particles at this point is a waste of time.

    As purely an amateur I fully admit I am in way over my head. In 2017 I read an article about a paper (unfortunately I never got to read the actual paper, can't find it now) where scientists at LHC had unexpected results of two photons being produced. The article didn't say the expected results, but it did say that paper suggested that gravity maybe acting in extra unknown dimensions (I mean mathematical dimensions, not Sci Fi alternate realities). If this is the case isn't it possible that Dark Matter does not exist and scientists are just casing a red herring. My point to this is that if experiments are producing results like this surely the results need to be fully explored before we start looking for something that we are not sure if it exists or not.

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    1. Simon,

      You are probably referring to the 'diphoton anomaly' of 2015. This anomaly had vanished by 2016. (I tell the story in my book.)

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  28. It is a part of the modern thinking of "bigger, larger, faster, wider, stronger, energy-richer", how to problems could be allegedly solved. It's the impasse of infinity. You will never reach an end, let alone new insights with reasonable efforts.

    Why not better starting thinking and rethinking?

    Throwing the money into independent and unconventional brains would bring more reliable results.

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  29. Lack of spacetime

    we look for dark matter, but we can`t find it. Dark matter is supposed to curve the spacetime as we see it. Wouldn`t it be the same to search for the "reason for the lack of spacetime" that we observe?
    That means wouldn't it be the same if there were some dark matter somewhere IN the galaxies/clusters or a lack of spacetime somewhere OUT of the galaxies/clusters?
    And, by the way, how do we know that the empty space would be flat (or even exist)?

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  30. The cost of the LHC is justified by the discovery of the Higgs boson, even if nothing else is found by it. But you're right that spending money on an even bigger collider makes little sense until we have a real theory, like the Higgs field theory, that makes precise enough predictions about alleged dark matter that it could actually be used to test, or falsify the theory. Until such a theory arises, there's no point in building something that we can't even rely upon to test it.

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  31. There's one geometrical alternative to dark matter that I haven't seen anybody mention. For at least half a century, some cosmologists have found it useful to connect cosmological expansion with timeflow, by treating the geodesic radius of the universe at a given spacetime point as a "proper time" coordinate ("a").

    If we take this approach literally, and say that expansion rate is a function of rate of timeflow, then the regions between galaxies, with slightly less gravitational time dilation than galaxy interiors, will expand faster, making then slightly more rarefied, and further increasing their local rate of timeflow and expansion, as a positive feedback process, so that a small initial imbalance becomes larger and larger.

    If the rate of timeflow in the regions between galaxies is greater (and the local gravitational field strength is lower) than the idealised "flat-floor" average that we might usually be tempted to use, then we get stronger galactic gravitational lensing effects and weaker galactic inertial coupling, allowing rotating galaxies to behave as more inertially self-contained systems.

    In other words, rather than strengthen galactic lensing and cohesion by increasing the field density //inside// galaxies (requiring dark matter), we can achieve a similar effect by //reducing// the field strength //outside// galaxies.

    And we already arguably have a purely geometrical rationale for wanting to do this, even if we //didn't// have any of the observational evidence that prompted the dark matter idea.

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