8. Is LambdaCDM or standard cosmology a 4th order speculation, and ought it be further researched ?

On August 9th, 2010  Prof. Abraham Loebfrom Harvad University  published a stimulating paper on the electronic preprint server with the title “Taking “The Road Not Taken”: On the Benefits of Diversifying Your Academic Portfolio“.

In this paper he takes issue with which type of research ought to be supported, making the much noted suggestion that innovative projects not following the main stream should be invested in by young researchers, in addition to following more secure research directions.  Abraham points out that even if one in a million new ideas bear fruit, this may completely transform our understanding of reality justifying the entire effort of using a certain fraction of funding for new, risky ideas.  To achieve this goal, he recommends that each researcher should spend up to about 50 per cent time on non-standard research, while individuals will naturally develop their own strategy based on personal and social factors. His suggestion is further that senior members of the community should find better strategies for rewarding innovation.

How does this fit in with the dark-matter versus non-Newtonan/Einsteinian dynamics issue?

Indeed, Abraham suggests MOND is a worthwhile non-standard approach in his Fig. 2. In his paper, Abraham states that “Once experiments push the upper limit on the cross-section of Weakly-Interacting Massive Particles (WIMPS) down well below the expectation of most reasonable models, alternative gravity models might apear more apealing.”

But, towards the end of the paper Abraham notes that the approach to cosmology via MOND plus neutrinos (as hot dark matter, see e.g. Angus, Famaey & Diaferio 2010) ought to be avoided as a non-standard research field because MOND and neutrinos are each individually unlikely to be true and thus the combination of both constitutes second-order speculative science.

The general gist of Abraham’s paper finds agreeement with many researchers, and has been commented upon very positively in discussions we are aware of.  For example, at the ESO coffee round, the rough notion of each researcher spending about 10 per cent time on non-standard research was talked about, based on Abraham’s paper.

But, there are two issues with Abraham’s statements:

One issue is that LCDM (i.s. standard cosmology) has been found to already fail on galaxy and somewhat larger scales (Kroupa, Famaey, de Boer et al. 2010), such that the CDM (cold dark matter) part must be wrong. Thus, WIMPS can’t exist. If some experiment were to find evidence for CDM particles, then the failure of LCDM would not be removed, but instead, the situation would become even worse in trying to understand how structures arise in the universe. This is straight-forward logics and has nothing to do with apparently not understood small-scale baryonic physics.

The other issue is that by removing MOND plus neutrinos from the recommended innovative research effort a logical error is made, as noted by Dr. Garry Angus: the current version of MOND and hot dark matter in the form of neutrinos are logically a unit. So, is MOND plus neutrinos a feasible alternative that ought to be followed seriously and supported by the senior scientists?

Abraham does not think so.

Following this paper,  Prof. Pavel Kroupa from Bonn University, while a Visiting Scientist at ESO headquarters in Garching, took the liberty to directly contact Abraham Loeb, applying the logics of Abraham and thereby raising the question whether LCDM (i.e. standard cosmology) should then not also be viewed as nth order speculative science (since it relies on not well understood speculative additions to physics such as inflation, dark matter, dark energy and the dark force – Kroupa, Famaey, de Boer et al. 2010). In this case n=4, ignoring the worrying issue that we do not understand how space-time and matter are coupled at a fundamental level within the LCDM framework.

Following Abraham Loeb’s reasoning, should the LCDM model not be also put on the list of research topics far too risky to bear any chance of success?: given the low probability that any one of the additions are true, the LCDM model is essentially ruled out to yield a correct description of the universe. And indeed, do the failurs of LCDM not already demonstrate this as a fact?

The following documents the e-mail exchange. Contributions are by

  1. Prof. Pavel Kroupa (16.08., 3:16pm)
  2. Prof. Abraham Loeb (16.08., 5:44pm)
  3. Prof. Pavel Kroupa (16.08., 6:28pm)
  4. Dr. HongSheng Zhao (16.08., 6:56pm)
  5. Prof. Mordheai Milgrom (17.08., 10:30am)
  6. Prof. Abraham Loeb (17.08., 1:23pm)

Interesting to note is that Li & Zhao (2009) have developed a theory which unifies the success of LCDM and MOND (see the 4th contribution below).

Feel free to add your comments below on how research is to be supported such that progress is maximised, or on what you think is worthwhile science.

Note also the discussion on this same topic concerning the US American Decadal Survey on which astronomy projects ought to have priority in the coming ten years.

1. e-mail on 16.08., 3:16pm:  Pavel Kroupa  —>  Abraham Loeb

Re: Taking “The Road Not Taken”: On the Benefits of Diversifying Your Academic Portfolio (by Abraham Loeb)

Dear Abraham,

Your recent posting on astro-ph was noted with interest in various places, and was also discussed here at ESO/Garching during coffee. Your suggestion that a fraction of ones’ research work ought to be spent on non-main stream ideas was received with quite some enthusiasm.

However, towards the end you single out MOND and neutrinos as a field of research which ought to be omitted, and you declassify this as “second-order speculations”.

I note this with interest, because it seems logically inconsistent with the rest of the text. And given this, it would cast doubt on whether your personal judgements can be trusted in terms of judging what ought to be done.

It is an established empirical fact that galaxies are MONDian objects. If you prefer to explain galaxies with cold or warm dark matter instead, then you are stuck with the second order speculation that the dark matter physics is dictated by the baryons. That is, you end up having to postulate the existence of a dark force Kroupa, Famaey, de Boer et al. 2010), in addition to all the other speculations in the LCDM model (e.g. Shanks 2005).

Having a hot dark matter component in the universe is also a fact. Neutrino oscillations imply the existence of an additional particle through the seesaw mechanism which may be a more massive contributor to hot dark matter and so hot dark matter with some dynamical importance seems to be in fact well motivated.

Furthermore, from what I have seen the physics community working on in the field of non-standard gravitation is following most beautiful approaches with deep implications for our understanding of space time and mass. I lack this in the LCDM community.

In fact, following your suggested argument: each of the individual speculations making up the LCDM model has a small probability of being true. One would consequently have to deduce that students and young postdocs should stop working in this field.

Therefore your statement is not understandable, and perhaps you could please clarify what you mean by excluding MOND from your list of non-main-stream physics research.

With kind regards, Pavel Kroupa

2. e-mail on 16.08., 5:44pm:  Abraham Loeb   —>  Pavel Kroupa

Dear Pavel,

Thanks for your e-mail. Over the past week I have received many more messages than on any of the few hundred papers that I posted on astro-ph in the past. My article must have touched a nerve in the community and I am grateful to messages such as yours.

As Moti Milgrom can tell you, I am very much in favor of exploring MOND because I am open-minded that it might represent the truth. However, I do not regard it as a mainstream theory as of yet. MOND is more successful than LCDM in explaining the dynamics of stars and gas within galaxies, but it is not as successful as LCDM in fitting the many cosmological data sets that were assembled over the past decade. Note that the bar for a successful cosmological theory has been raised dramatically since the 80s when Moti wrote his first insightful papers about MOND.

My sense is that if MOND is right, then it must have its underpinning in an elegant new theory of nature. The current limits on neutrino masses (<1eV) imply that thermal neutrinos make a small contribution (<1%) to the global mass budget in X-ray clusters. Moreover, the acoustic oscillations in the CMB anisotropies were detected now up to high harmonics and would be difficult to reconcile with the simplest MOND+neutrinos cosmological model.  Baryonic oscillations are observed in galaxy surveys of the present-day Universe at exactly the correct wavenumber that LCDM predicts (based on the response of collisionless dark matter to the imprint of the radiation sound waves on the distribution of baryons at recombination).

I am personally torn between the success that MOND has inside galaxies and the success that LCDM has on cosmological scales.  Most of the cummunity prefers to believe that LCDM will explain galaxies once we understand the complex feedback processes there. But in my mind, it is also possible that LCDM will be replaced by a generalization of MOND to the cosmological context. However, I regard neutrinos as a speculative addition to both MOND and LCDM. The classification of LCDM as a “bond” in my article is based on the much greater popularity of LCDM among cosmologists. As we know, the truth is not always popular. But my current sense (based on all available data) is that MOND could turn true only through a conceptual breakthrough rather than by adding a speculative matter component.

With best wishes,

3. e-mail on 16.08., 6:28pm:   Pavel Kroupa   —>   Abraham Loeb

Dear Avi,

Thank you for your prompt clarification.

I agree with you on all accounts, but take a much stronger and clearer standpoint, also in view of your published statements:

MOND is an overwhelmingly more successful description of the universe where detailed observations on cosmological scales (i.e. galaxies and even clusters) can be made. Even on galaxy cluster scales MOND is only missing a factor of two in mass, and this is nearly a factor of one already.

So research dealing with MOND or related ideas is what ought to be supported very strongly, even at the expense of funding for LCDM work.

LCDM work has led to no successful progress whatsoever on these well-observed scales since more than ten years, and the situation has been deteriorating constantly. In fact, I am amased to have realised that every prediction that the CDM-Ansatz has made has failed, while virtually every MOND prediction I am aware of has been successfully verified through observation. So please excuse my complete ignorance here, but as a scientist it ought to be quite clear which direction ought to be considered the better one, in terms of future funding.

That LCDM is successful on large scales, as you write (where observations are so much more difficult) is somewhat overstated, and even if true, it does not mean that another theory would not also explain the observations (some of which are still debatable though, e.g. recent Sawangwit and Shanks contribution on the CMB).

So your conclusion/suggestion in your astro-ph posting is not helpful at all, I am sad to write. It resonates with those strongly opposed to MOND (and there are many indeed). You will realise that the funding situation is not helped given statements such as you are making, and this can be deemed as being damaging in the historical context, because progress is slowed.

Imagine that 10% of the funding available for LCDM work would be channelled into MOND plus neutrino work. We would get much better quantifications of whether this ansatz works as well or even better than LCDM on large scales. Or, with that level of funding, entirely new theoretical avenues might be found that give MOND. But this is not happening.

That MOND works endlessly better than LCDM on galaxy scales is already an established fact. But all I hear is that funding is not being granted for “second order speculative” science, or that “second-order” scientists are not hired on faculty positions, or that MOND research at a Max-Planck Insitute is not seen to be worthwhile. In trying to understand galaxies even better, we are at this very moment faced with the problem of possibly loosing many years of research effort in galaxy modelling in MOND, simply because funding is not upcoming to keep those with the knowledge in the job. At the same time, many hires are taking place for numerical experts within the LCDM framework, although we already know that LCDM does not work.

This is a disaster from the point of view of how tax-payers money is being used to advance our understanding of nature. It is a dark epoch in the history of science, and the only reason the tax payer does not revolt is because they cannot understand the complex issues at hand.

Best wishes, Pavel

4. e-mail on 16.08., 6:56pm:

HongSheng Zhao  —>  Araham Loeb and Pavel  Kroupa

Dear Avi and Pavel,

Part of your debate seems to be around the (in)feasibility of unification of LCDM and MOND.

I invite you to read an example of such a co-variant generalization of MOND to do (most of) the job of LCDM at large scale without throwing away MOND’s advantage on galaxies.  This model uses same number of fields (vector+scalar) as TeVeS, but these fields explain more phenomena than TeVeS did, e.g., offering an explanation of the Lambda phenomena for free.  The scalar field explains the CDM phenomena in large scale and high density, and its effect is tapered away in galaxies.  We didn’t use a single non-baryonic (neutrino) particle, at least not explicitly in this formulation.

Environment-dependent dark sector” in Physics Rev. D, by Li and Zhao

Comments welcome.


5. e-mail  on 17.08., 10:30am:   Mordehai Milgrom  —> Abraham Loeb

Hi Avi,

Your points are all well taken, at least qualitatively. But I think I would put rather different weights on the different pieces of evidence.

In the first place, to use your own assertion, remember that the bar for successful GALACTIC theory has also been raised dramatically since the time of the first MOND papers. Few people remember, in fact, that when I proposed MOND, and some years after that, there was not a single MOND rotation curve analysis.

The first rotation curve test of the MOND predictions was done only in late 1987 (by Steve Kent), more then 4 years after the advent of MOND, because they had had to await the extended HI rotation curves. And, of course, we have gone a very long way since then. (The TF relation was also not well established then).

I would also remember that every time the bar in cosmology was raised significantly, a new adjustment of the “theory” has had to be made to adjust to the new bar (e.g. the introduction of dark energy, and the huge change in the DM content of the universe from 95% to ~ 20%), while MOND has not required a single adjustment at regards galactic phenomenology from its first day.

Also, when comparing the weight of the MOND successes on galactic scales with those of LCDM in cosmology we should bear in mind the following:

1. I think that, epistemologically, there is far more independent data to be predicted in the context of galactic astronomy then there is in what we call cosmology.

While a single galaxy is certainly not as “important” as the universe at large, each galaxy, in the data sense, is an independent universe.

Roughly speaking, the gravitational field of a galaxy is a function of three variables, while the whole of what we call cosmological data today barely comes to that much. (This is only a rough caricature, of course).

For example the whole CMB really comes down to a few parameters to be explained related to the positions of the first few peaks and their relative heights,  there are also several parameters that go into the fitting.

For example, I think the evidence for cosmological DM in this context is based mainly on the relative height of the third peak. I am very far from disdaining the successes of the standard cosmological model, but I think we should not lose sight of what is involved in this success.

CDM advocates indeed say they hope one day to explain away the apparent contradictions of their predictions with the data on galactic scales. But surely they cannot hope to actually predict, for example, the rotation curve of a  given galaxy from only its baryon distribution. How can they when the relation between baryons and CDM distribution, which largely determines the RC, depends so much on the turbulent history of how this particular galaxy was shaped (mergers, dissipation, feedback, supernovae, etc.)? a history that can never be known. (Tidal dwarfs are the only exception I know of. There, the expected DM content is known because it is determined by a single recent event that erased the past history. As you may know CDM does not fare very well there.)

2. For CDM in the context of galaxies, the basic theoretical ingredients are known already (unless you  want to invoke a non CDM picture)  and that is what you have to work with.

For MOND in the context of cosmology we still have many open possibilities theory-wise.

I personally think that TeVeS (Bekenstein 2004), with all the good things that it does give us, is not really the answer.

BIMOND (Milgrom 2009) has only been explored very superficially in this context. And I agree with you: MOND needs a  fundamental theory, probably based on principles and ideas not thought of heretofore.  But I think we could make a judgment based on what MOND does already do.

We do not need to have a theory of quantum gravity to be rather sure that there is fundamental truth in GR, even if it is most probably not the whole truth.

All the best, Moti

6. e-mail on 17.08., 1:23pm:  Abraham Loeb  —>  Pavel Kroupa


This would be fine with me. [putting up this blog]

You might want to correct a statement you made in your last e-mail (or
simply include this e-mail in the blog). I am not stating that MOND is
second order speculation, but that MOND+neutrinos belongs to that
category. MOND (together with all theories of modified gravity) is
mentioned as Venture Capital in Fig. 2 of my article.


by Anton Ippendorf, Pavel Kroupa and Marcel Pawlowski (18.08.2010): “Is LambdaCDM or standard cosmology a 4th order speculation, and ought it be further researched ?” on SciLog. See the overview of topics in  The Dark Matter Crisis.

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2 thoughts on “8. Is LambdaCDM or standard cosmology a 4th order speculation, and ought it be further researched ?

  1. a further e-mailHi Avi,
    To the extent that what you have written is advice to junior scientists, I
    think your advice is spot on. You are, after all, encouraging them to be
    *more* adventurous, not less. And I agree with your assessment of the
    sociology of the situation, which is of course distinct from the science. To
    the average practicing cosmologist, I expect MOND+neutrinos does sound like
    the product of two epsilons. It sounds odd even to me. But that is a
    sociological statement based on where we are coming from, and has nothing to
    do with where we need to get to. Mostly I find it sad the the field has not
    come much further in this regard.
    You remark on the scale of the BAO being particularly noteworthy, and it
    is. But as Moti points out, so is the predictive power of MOND in galactic
    dynamics. Why does it seem that no one is trying to understand this? If
    the cause of MOND’s predictive successes is not MOND itself (the rather
    obvious answer), then the phenomenology is still telling us something
    important. Yet the most common answer from cosmology seems to be “well,
    galaxies are complicated, non-linear things, and therefore we should be
    absolved of understanding them.” But the behavior is not complicated. It
    is simple. So simple that it can be written in one formula – the one that
    Moti found decades ago. I have found this to be very hard to understand in
    the context of dark matter: MONDian phenomenology does not emerge naturally
    from LCDM, despite the occassional assertion that surely it must work out.
    Somehow. More commonly, this well-established, observed phenomenology is
    simply ignored. I don’t see how we’re going to arrive at a satisfactory
    theory by ignoring inconvenient phenomena.
    best regards,


  2. The problem is not roads, it is the Emperor’s New Clothes:http://arxiv.org/abs/astro-ph/0510535
    Is Modern Cosmology the Emperor’s New Clothes?
    4 Conclusion
    1. The well-known fact can not be ignored that gravity is very very weak. For example, it is 10^{−40} times weaker than the electricity between protons. Therefore, humans in the foreseeing future can not design a physical precision experiment which can resolve the 10−40 strength of the earth’s gravitational field. That means we have not had a full understanding of gravity. But scientists assume they had it
    and applied the preliminary results of Newton and Einstein to the whole universe. This resembles the situation of cycles and epicycles in the old geocentric model.
    2. It is a fact that the results of Newton and Einstein deal with the motion of two-bodies. When applied to the free motion of many-bodies, the theories give chaotic results. However, the universe
    has orderly motion. Whenever a problem involves free many bodies, Newton and Einstein theories have no power. For example, the Bode law of planetary distribution in the solar system has not been explained.
    3. Newton and Einstein theories have no power for the explanation of natural structures. Galaxy structure is the simplest one in the observational world. Every one with common sense must suggest
    that there exists a law on galaxy structure. Newton and Einstein theories can not provide such law because they are the theories of two-bodies. The law is very possibly the rationality explained in my article.
    4. The mainstream model of the universe (the Big Bang theory) which is based on Newton and Einstein theories, is being declined. A new article (Nieuwenhuizen, Gibson & Schild (2009)) describes:
    Nearly every month new observations arise that pose further challenges to the CDM paradigm: Correlations in galaxy structures (Disney M. J. et al. (2008)); absence of baryon acoustic oscillations in galaxy-galaxy correlations (Sylos Labini, Vasilyev & Baryshev Yu (2009)); galaxies formed already when the universe was 4 to 5 billion years old (Bouwens & Illingworth (2006)); dwarf satellites that swarm our own galaxy just like its stars (Metz M. et al. (2009)). Observational data (Kroupa et al. (2010), Peebles & Nusser (2010)) strongly suggest a paradigm shift for cosmology.


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