Friday, October 03, 2014

Is the next supercollider a good investment?

The relevance of basic research is difficult to communicate to politicians who only care about their next term and who don’t want to invest in what might take decades to pay off. But it is even more difficult to decide which research is the best to invest into, and how much it is worth, in numbers.

Whether a next supercollider is worth the billions of Euro that it will eat up is a very involved question. I find it partly annoying, partly disturbing, that many of my physics colleagues regard the answer as obvious. Clearly we need a new supercollider! To measure the details of this, and the decay channels of that, to get a cleaner signal of something and a better precision for whatever. And I am sure they will come up with an argument for why Susy, our invisible friend, is still just around the corner.

To me this superficial argumentation is just another way of demonstrating they don’t care about communicating the relevance of their research. Of course they want a next collider - they make their living writing papers about that.

The most common argument that I hear in favor of the next collider is that much more money is wasted on the war in Afghanistan (if you ask an American) or rebuilding the Greek economy (if you ask a German), and I am sure similar remarks are uttered worldwide. The logic here seems to be that a lot of money is wasted anyway, so what does it matter to spend some billions on a collider. Maybe this sounds convincing if you have a PhD in high energy physics, but I don’t know who else is supposed to buy this.

The next argument I keep hearing is that the worldwide web was invented at CERN which also hosts the LHC right now. If anything, this argument is even more stupid than the war-also-wastes-money argument. Yes, Tim Berners-Lee happened to work at CERN when he developed hypertext. The environment was certainly conductive to his invention, but the standard model of particle physics had otherwise very little to do with it. You could equally well argue we should build leaning towers to advance research on general relativity.

I just finished reading John Moffat’s book “Cracking the Particle Code of the Universe”. I can’t post the review here until it has appeared in print due to copyright issues, sorry, but by and large it’s a good book. No, he doesn’t use it to advertise his own theories. He mentions them of course, but most of the book is more generally dedicated to the history, achievements, and shortcomings of the standard model.

His argument for the relevance of particle colliders amounts to the following paragraph:
“As Guido Altarelli mused after my talk at CERN in 2008, can governments be persuaded to spend ever greater sums of money, amounting to many billions of dollars, on ever larger and higher energy accelerators than the LHC if they suspect that the new machines will also come up with nothing new beyond the Higgs boson? Of course, to put this in perspective, one should realize that the $9 billion spend on an accelerator would not run a contemporary war such as the Afghanistan war for more than five weeks. Rather than killing people, building and operating these large machines has practical and beneficial spinoffs for technology and for training scientists. Thus, even if the accelerators continued to find no new particles, they might still produce significant benefits for society. The Worldwide Web, after all, was invented at CERN.”

~ John Moffat, Cracking the Particle Code of the Universe, p. 78
Well, running a war also has practical and beneficial spinoffs for technology and training scientists. Sorry John, but that was disappointing. To be fair, the whole book itself makes a pretty good case for why understanding the laws of nature is important business. But what war doesn’t do for your country and what investing in basic research does is building a base for sustainable progress. Without new discoveries and fundamentally new insights, applied science must eventually run dry.

There is no doubt in my mind that society invests its billions well if it invests in theoretical physics. Whether that investment should go into particle colliders though is a different question. I don’t have a good answer to that, and I don’t see that the question is seriously being discussed. Is it a worthy cause?

Last year, Fermilab’s Symmetry Magazine ran a video contest on the topic “Why particle physics matters”. Ironically most of the answers have nothing to do with particle physics in particular: “could bring about a revolution,” “a wonderful model of successful international collaboration,” “explore the frontiers and boundaries of our universe,” “engages and sharpens the mind”, “captures the imagination of bright minds”. You could use literally the same arguments for cosmology, quantum information or high precision measurements. Indeed, I personally find the high precision frontier presently more promising than ramping up energy and luminosity.

I am happy of course if China will go ahead and build the next supercollider. After all it’s not my taxes and still better than spending money on diamond necklaces that your 16 year old can show off on facebook. I can’t quite shake the impression though that this plan is more the result of wanting to appear competitive than the result of a careful deliberation about return on investment.

36 comments:

Robert L. Oldershaw said...

It seems to me that other branches of physics are contributing much more to the progress of meaningful discoveries about physical reality, as opposed to generating ambiguous and far too indirect pseudo-tests of shaky models.

Uncle Al said...

Hadron ring colliders are astoundingly inefficient. Hadron collisions distribute energy among their partons. A proper international investment

1) is a long swath of politically stable, flat, unusable land (e.g., Southwest Australia);
2) is a dedicated multi-gigawatt reactor complex for energy (sell excess);
3) is a face-to-face linear lepton collider;
4) is 1000 TeV lab frame collision energy;
5) admits 105.6583715 MeV/c^2 muons versus 0.511 Mev/c^2 electrons;
6) requires fast acceleration (short/energy). Unruh effect studies;
7) considers the two-beams' (100 - epsilon)% that does not collide.

http://practicalaction.org/images/events/publicgood-king-7.gif
Local affluence reproduced into global penury.

Don Foster said...

As for a ‘bang for the buck’ rationale, I think it is China that requires aspiring architects to work a year in construction before beginning their academic studies.

One billion dollars would fund ‘sandbox sabbaticals’ for 100,000 physics graduate students. Maybe we missed something along the way.

Thomas Schaefer said...

The argument about war spending is of course nonsense. (If it had something to do with security, it would be money well spent. If not, then why not spend it on education, health, or any number of good causes.) The argument about the web is a little better, because at least it is a valid reason for spending money on science in general.

An oversimplified model of funding decisions is that society allocates money to science, a combination of society and scientists allocates money across fields, and scientists allocate money within their discipline.

How society allocates money to science is really a mystery, and certainly something of a combination of historical accidents (WWII, the growth of the modern research university, sputnik). How we allocate money across fields is also strange, a combination of political and societal pressures (health), the university system (the need to teach physics and calculus to engineers).

Allocation across subfields is, to first order, driven by demographics (how many CM, HEP, AMO, NP scientists). There is a difficult chicken & egg problem. Do people follow funding, or does funding follow people?

Allocation within a subfield, here HEP, is in principle (but not in practice) straightforward. People get into a room and prioritize. The US just went through this sort of exercise, and the next generation of large circular colliders is a priority, but not the only one. This is a problem, because the money involved clearly exceeds the amount currently allocated to HEP (which has been shrinking in recent years). This means we either take our case directly to the public (making silly arguments about the war and the web), we take a slower road trying to grow the field, or convince colleagues in other fields (Hmm), or we hope that some country in east asia will pay for it as a matter of national pride. This appears to be the current strategy.

L. Edgar Otto said...

Excellent topic, thanks for caring.

To lose touch with particle physics is to lose touch with the very core of what we are, but as individuals and the collective take their turn at the next tooling phase the old eras are surpassed and we get caught up in the scars of wasteful building - it is more than such national issues but it is that also. Thing is losing touch like this we may not know better between those rare times of golden ages and long winters in the dark.

Arun said...

I think the case for another supercollider depends on what the current one finds.

Alejandro Rivero said...

Yep, the "a lot of money is wasted anyway" argument is wrong even at the rhetoric level: it carries the collateral message that particle research is wasted money too.

CapitalistImperialistPig said...

The golden age of particle physics was the child of the nuclear weapon. Governments poured money into accelerators because they knew that nuclear physics had given birth to this monstrous progeny and feared that somebody else might free the next even more terrible genie first.

The best remaining argument is probably that of Faraday, who, when asked what the use was of electromagnetism (by a Prime Minister) replied "I don't know, but someday you will tax it."

Of course there is the prestige factor - governments still spend billions on Olympics, World Cups, and space missions.

Plato Hagel said...

I guess one might want to ask whether a new supercollider design could help Alice further its' exploits on the subject of the Quark Gluon Plasma?

So you say super, but also, its the next generation, you see?:)

L. Edgar Otto said...

Plato Havel, very good point. This is the frontier issue where the contribution of total mass in 4D is an alternate SUSY concept.
So the LHC as not finding super particles gives us a little better certainty of theory direction if not that it still might.
While these machines plausibility cannot make the earth vanish the overall symmetry may still have cutting edge surprises economic and military concerns model to worry about for unseen surprises.
So far these are issues of thermodynamics in the main. But can the quark-gluon plasma exist as in the heart of stars or only be indirectly observable? Or for the avoidance if not resistence by string theorists of such concepts they are blind to them even in theory instinctively.
Thus string theory cannot claim to be the heir of quantum mechanics.
We may need some new particle terms, say a quon-glark plasma.
Now general mass from motions aside as the greater contribution of total mass or corresponding statistical methods aside the invoking by half the mass from tauons to 4 forces up to the Higgs contribution, this SUSYQ also needs more from 5D concepts in this world of forces summed and squared. Here we may find a neutral exact mass-gravity ubiquitous equivalence and better mathematical models for all scales and hierarchies.
I do not mean not to cite others for some of these ideas here but I can only see one blog or paper at a time. And to argue for the case a few more simple concepts are needed if decisive. An asymmetric superdetermined time particle may be recursively needed too.

Sabine Hossenfelder said...

CIP:

Yes, I understand the prestige factor, there is also plainly entertainment etc. Space missions are a good example. I don't really see what's so terribly interesting about rocks, regardless of whether they are on Earth, on Mars, or flying through space, and the same goes for dust. For what the physics that I am interested in is concerned I find space missions pretty useless (I don't mean satellites and telescopes of course). But arguably people get very inspired by it and that I think is totally worth the money. Best,

B.

Sabine Hossenfelder said...

Don,

Yes, that's basically my thinking - Instead of spending 10 billions on one high risk project, why not make it 1000 smaller high risk projects. There are many not-so-spectacular but comparably inexpensive missions that at least in my eyes seem equally worth the money. The main reason (not that it's the only reason) that there's so much money being put into high energy particle physics is for all I can tell that there are a lot of particle physicists. It's a historical thing and I'm afraid we'll get stuck with that at some point. Best,

B.

Sabine Hossenfelder said...

Arun:

Well, if you believe what the Chinese said (see Nature article that I mentioned) then they're set to build the next one, regardless of what the 2015 run will bring. Best,

B.

Zephir said...

I can fully agree with Bee in this regard. My opinion is, the future colliders will just increase the noise/signal ratio of experimental data, but it will not bring any substantial progress. It's because our Universe looks like the fractal landscape under the fog - at certain distance the more intensive shining of light into it will not bring a better resolution of details. The astronomers already realized with stopping of building of large telescopes in optical spectrum.

The SUSY models (which ignored the inversion of space-time in their derivation) manifest itself at low energies, not these extreme ones. Also, the evidence of extradimensions of stringy theories is as easy as the detection of forces violating the inverse square law - no high energy colliders are required for their detection. The microblack holes were observed routinely with formation of atom nuclei at Tevatron and LEP before many years already.

Even Stephen Hawking (who promoted the LHC carelessly just before few years) suddenly did become catious regarding the future supercollider experiments.)


In addition there is whole spectrum of scalar wave physics belonging to realm of quantum gravity, which doesn't require the building of any expensive machines, dissipating the irrecoverable resources of helium and precious metals. We should research smarter, not harder and the HEP physicists seeking the fame should find a more useful jobs, for example in cold fusion research. The decadent ignorance of contemporary physics (which is facing the energetic crisis) manifests itself right here.

johnduffield said...

I think "big science" colliders and their associated collaborations have rather painted themselves into a corner with the Standard Model. There's no interfacing with other fields/models in order to improve it, and there's too much pimping of busted-flush SUSY to a public and politicians growing increasingly exasperated at how useless it all is. Since a new supercollider would only perpetuate this, I just can't see it happening myself. I'd go so far as to say CERN is doomed unless it can break the impasse and demonstrate some progress.

Amos said...

This week's issue of The New Yorker magazine includes a cartoon with the caption "Once you have a collider, every problem starts to look like a particle."

Plato Hagel said...

I mean, your article is in my thoughts.:)

Don't you see how you move forward? Once you combine the phenomenology and do the experiment, the result takes you a little further?

Best,

L. Edgar Otto said...

Andrei,
your comment seems to me both contradictory and illogical (if in some sense any of our thoughts brought to the table mean anything.)
It is not a question of more bang for the buck or more rumble for the ruble. To invest in metals like free electrons is a tightrope path over all atoms, not an exchange of electrons between them.
Is the future plastic or ceramic, or either the past as we fall from the rope on either side?
Is there really a difference (as Hoyle said of the quasars "Perhaps the universe is many little bangs instead of one big bang ") so too of big and many science projects in cycles.
Survive is s ceramic concept at odds with a future of ever more vaporous plastic wealth becomes as complex economics builds its power based on insurance that taxes people's fear.
The focusing of energy to an ever finer nano scale as in colliders or the search for deeper definition of detail will converge to the same theory animal. Omnipotent Higgs reads to me as a bad metaphor (worse than the materials one I just offered here) and simply bad physics.
Given opportunity and responsibility so many great minds find the terrible price as waste. You have not shown proof but sense something beyond the scope of frontier physics just a whisper of the depth of complexity. To make a breakthrough the thing not given already in this universe is time enough to so explore.
But it reads saner to me than Lubos who does not know he contradicts himself on split foundations.
Good luck on your given half random walk to surpass horizons in wisdom even if our mathematicans just begin to imagine wider physics off diagonal and arbitrary states of privilege views.

qsa said...

What If We’re All Wrong?
What terrifies theorists is that the LHC may discover nothing beyond the single neutral “Higgs” particle that is required by the standard electroweak theory. With no sign of supersymmetry or technicolor or anything unexpected, we would then have no clue to what happens at the much higher energies where gravitation becomes a strong force. We fervently hope for some complicated discoveries.
—Steven Weinberg, Nobel Prize winner, University of Texas at Austin


http://seedmagazine.com/content/article/why_a_large_hadron_collider/

Is there a similar statement for the new collider.

L. Edgar Otto said...

Something that in the middle scale of things, as if fixed yet not toward ultraviolet or infrared at least begins as a ready made laboratory just as some have said of higher energy cosmic rays as nature's collider.
This is our biological nature of which the origin of life or its ultimate direction we may imagine so ask yet beyond cosmological and standard models some next big experiment and vision may ellude us. We then can say only life is as too simple to see despite its endless depth of complexity.
But the accessible question remains near us - Why does evolution INVEST so much in costly replication?
Life itself seems to explore many models as analogs to our evolving understanding of physical laws.
A male cricket falls apart after fertilization to provide food for the offspring and energy for the female. The mother squid protects her giant eggcase until the hatching then falls deeper into the deeps, her work done.
Life seems at least a mindless vital force as does the flow of time but I have little doubt we will find better and useful physics beyond supersymmetry or (random?) walking Technicolor as our research comes closer or becomes one with the mystery of our being as light's source.

Stuart said...

Sabine sorry if this may sound off topic. It is a question about possible lorentze invariance violation in close proximity to blackholes. Here is an interesting scenario.Say Alice takes her photon clock (one which keeps track of time by bouncing a photon between a pair of mirrors) next to a black hole and Bob observes the clock from a distance.Since the clock slows down in strong gravity will Bob see photons bouncing up and down the mirrors at speeds less than light? If so then this will be lorentz invariance violation.

Giotis said...

I strongly disagree with such opinions and for me at least they are anathema; essentially arguing against a bigger machine is arguing against reductionism and we know that reductionism works.

Zephir said...

/*...and we know that reductionism works...*/

IMO the reductionism worked only in universe geometry, in which the number of dimensions decreased with increasing energy scope - but the contemporary technological progress already passed this boundary. In AWT now we can only prove, that the Universe is intrinsically random system. The question is, if such a finding is worth of these gigantic investments. In this matter the interests of crowds of physicists get into collisions with the rest of human society, which is paying their fun. IMO the much more interesting findings is still lurking at the much weaker energy scales: the cold fusion and scalar wave phenomena - the physicists just must change their way of thinking for to realize it.

Sabine Hossenfelder said...

Stuart: Correct, the black hole spacetime is not globally Lorentz-invariant. Lorentz-invariance is only a global symmetry in flat space. Best,

B.

Matti Pitkanen said...


I cannot avoid the feeling that particle physics corresponds in the evolution of science to the end of the era of dinosaurs in biology. After dinosaurs with minimal brain size but gigantic body emerged mammals with small body and bigger brains.

I suspect that future generations start to ask hitherto unasked questions. Could dark matter be something more than few exotic particles? Is quantum theory in its recent form really final? Can we accept the problems of the quantum measurement theory and continue to say that quantum theory is just crazy? Is biology nothing but complexity? Can we really leave consciousness outside physics and could the understanding of consciousness require new physics and new quantum theory?

Successful answer to these questions might replace particle physics as the frontier of science with quantum physics of biology and neuroscience and make gigantic accelerators unnecessary.

Successful answer could also mean totally new view about the role of quantum gravity even in everyday world and allowing an escape from the recent dead end manifesting itself as endless debates about firewalls and existence of blackholes.

Plato Hagel said...

Hi Matti,

Successful answer to these questions might replace particle physics as the frontier of science with quantum physics of biology and neuroscience and make gigantic accelerators unnecessary.

Are you not sure that consciousness itself is not hidden in the idea of reductionism?

Also, from an abstract point of view, how much closer are you to the question given that we understand that we are conscious, but that we are still conscious as we explore using mathematical tools? Is your theories not based on elements of the abstract and correlations then found in other things to support your theory?

Successful answer could also mean totally new view about the role of quantum gravity even in everyday world and allowing an escape from the recent dead end manifesting itself as endless debates about firewalls and existence of blackholes.

When you probe the abstract one implores additional tools to introduce different elements into the abstract. A new way of looking at the theory?

Best,

Phillip Helbig said...

"After dinosaurs with minimal brain size but gigantic body emerged mammals with small body and bigger brains."

Bad metaphor. Dinosaurs were one of the most successful groups of animals, existing for hundreds of millions of years. Small-bodied, large-brained creatures can celebrate when they reach even 10 per cent of that time.

They did not die because of their small brains. Perhaps, to some extent, because of their large bodies, but keep in mind that at the same time many, many other species became extinct. The cause was external and had nothing to do with how successful they were on Earth.

"Dinosaur" in the sense of "old-fashioned, behind the times, too big for serious business" etc is a really bad metaphor. Few groups of animals have been as successful.

L. Edgar Otto said...

That we can know subconsciously which way we push a right or left hand button by six tenths of a second before we choose to consciously do in matching data in brain scans complicates the usual acid tests of free will. Stealth stops charged or neutral? Anti-stops?
Perhaps Lubos has rediscovered the brontisaurus pulling the wrong heads on the wrong bodies so long it needs a small brain in its tail to fend of the allosaurs in time independently.
So an elephant skull might suggest the myth of Cyclops or monopoles to primitive man.
Contrary to Dirac sound wave forms may be everywhere in nature. Now birds descended from dinosaurs noe sing much more intricately than we mammals can hear. But we can play sirens backward and surprise- some sounds become inaudible no matter if they are strong enough to rattle ones bones.
So to with models, an apt question of dinosaurs of symmetry issues as the metaphor. Dark matter anyone? Can you see it, can you feel it?
Before we can play entropy backwards
we need a better unified theory at least as advanced as Matti Pitkanin's gauge like insights.
We cannot have a propositional calculus that distinguishes tautology and contradiction and the total unity as superimposed quantum mechanics at the same time.

Zephir said...

/* Few groups of animals have been as successful. */

Nobody says, that the existing paradigms of physics weren't successful on their very own. I even think, that the individuals will never play the role of personality cult as successfully, as the physicists of Einstein's era.

L. Edgar Otto said...

Zephir, I sometimes feel that, at least for awhile anyway. The greatest generation that at first discourages those who would take up the new.

Well, beetles are rather successful. and The Bacteria have lasted the longest and reached the sky and depths of the sea. But damn it, they are just bacteria!

qsa said...

Science, Scientists, and the Science Budget

http://www.issues.org/19.4/updated/bromley.pdf

"Despite this increased present and projected access to federal policymaking, many scientists and engineers remain frustrated with science and technology policy at the federal level. I have spoken with more than a few who dismiss the process as narrowly political, as responsive largely to special interests. That has not been my experience. Policymakers need to balance a large number of objectives in arriving at sound policies, only some of which are based purely on scientific and technological criteria. If they are not successful in balancing these objectives, they risk damaging the science and technology enterprise."

http://www.oecd.org/science/sci-tech/1905250.pdf

MarkusM said...

There are obviously things that make way way more sense !

Georg said...

I guess,
progress in this field will rest on
Mythbuster TV Show.
The show will be called "Strings YES or No?", cost will be low due to their
famous ability to improvise, money
will come from Pay-TV. :=)
Georg

Stuart said...

@Sabine your answer has far reaching consequences for asymptotically safe quantum gravity. It implies that the graviton becomes massive at curvature radii less than the Hubble radius until at the Planck length it becomes a Planck mass Black Hole. If you Divide the Hubble radius by the Planck length you get 10^60 Eigen states that the graviton can assume. Thus the Planck radius is the UV cut off and the Hubble radius the IR cut off.

L. Edgar Otto said...

Stuart,

When we consider the contribution of mass from the Higgs to the tauons these are not clearly related as between any two successive generations. So the implications are far reaching indeed. The question is one of an interval of entanglement, that is what is the speed of gravity? We see recently in open systems it is four times the speed of light by which in effect we can see light at rest, that and the new particles of mixed strong force generations to suggest a little more than meets the eye by experiments. This may not sound as important as the Higgs idea but is perhaps one of the first achievements for the LHC, and a great case that we keep the machine maintained, build new ones when we can. In our time it should be said that like said before advanced technology is indistinguishable from magic, that our cosmic dreams with science a sanity for some thinkers like Peter Rowland and our host who sees a little further, that for the rest of us advanced technology is indistinguishable from our qualitative ideas of the vague term schizophrenia, in retrospect anyway.

Kaleberg said...

Maybe it is time for a pause before the next generation of particle accelerators is built. A lot of other things can change that will make the next generation more powerful and more useful.

Optical telescope development paused from the 1950s into the 1980s. At some point it didn't make sense to keep making bigger and bigger chunks of glass. Then new control systems and new fabrication techniques led to the current generation of increasingly huge composite telescopes.

It's impossible to predict just what breakthroughs would be necessary for a real next generation of accelerators. Obviously, there has to be a lot of energy and a lot of particles. Perhaps they'll recycle a failed fusion reactor design, but that's just extrapolating. Perhaps they'll take advantage of plasma interactions involving Jupiter's inner moons.

We haven't quite mined out what the LHC can do, and if Fermilab is any indication, we haven't built the last generation of experiments and detectors for the LHC yet. No one is eager to see particle physics close up shop completely, but there are so many other avenues to explore.