|The recently deceased diphoton|
bump. Img Src: Matt Strassler.
I finished high school in 1995. It was the year the top quark was discovered, a prediction dating back to 1973. As I read the articles in the news, I was fascinated by the mathematics that allowed physicists to reconstruct the structure of elementary matter. It wouldn’t have been difficult to predict in 1995 that I’d go on to make a PhD in theoretical high energy physics.Little did I realize that for more than 20 years the so provisional looking standard model would remain undefeated world-champion of accuracy, irritatingly successful in its arbitrariness and yet impossible to surpass. We added neutrino masses in the late 1990s, but this idea dates back to the 1950s. The prediction of the Higgs, discovered 2012, originated in the early 1960s. And while the poor standard model has been discounted as “ugly” by everyone from Stephen Hawking to Michio Kaku to Paul Davies, it’s still the best we can do.
Since I entered physics, I’ve seen grand unified models proposed and falsified. I’ve seen loads of dark matter candidates not being found, followed by a ritual parameter adjustment to explain the lack of detection. I’ve seen supersymmetric particles being “predicted” with constantly increasing masses, from some GeV to some 100 GeV to LHC energies of some TeV. And now that the LHC hasn’t seen any superpartners either, particle physicists are more than willing to once again move the goalposts.
During my professional career, all I have seen is failure. A failure of particle physicists to uncover a more powerful mathematical framework to improve upon the theories we already have. Yes, failure is part of science – it’s frustrating, but not worrisome. What worries me much more is our failure to learn from failure. Rather than trying something new, we’ve been trying the same thing over and over again, expecting different results.
When I look at the data what I see is that our reliance on gauge-symmetry and the attempt at unification, the use of naturalness as guidance, and the trust in beauty and simplicity aren’t working. The cosmological constant isn’t natural. The Higgs mass isn’t natural. The standard model isn’t pretty, and the concordance model isn’t simple. Grand unification failed. It failed again. And yet we haven’t drawn any consequences from this: Particle physicists are still playing today by the same rules as in 1973.
For the last ten years you’ve been told that the LHC must see some new physics besides the Higgs because otherwise nature isn’t “natural” – a technical term invented to describe the degree of numerical coincidence of a theory. I’ve been laughed at when I explained that I don’t buy into naturalness because it’s a philosophical criterion, not a scientific one. But on that matter I got the last laugh: Nature, it turns out, doesn’t like to be told what’s presumably natural.
The idea of naturalness that has been preached for so long is plainly not compatible with the LHC data, regardless of what else will be found in the data yet to come. And now that naturalness is in the way of moving predictions for so-far undiscovered particles – yet again! – to higher energies, particle physicists, opportunistic as always, are suddenly more than willing to discard of naturalness to justify the next larger collider.
Now that the diphoton bump is gone, we’ve entered what has become known as the “nightmare scenario” for the LHC: The Higgs and nothing else. Many particle physicists thought of this as the worst possible outcome. It has left them without guidance, lost in a thicket of rapidly multiplying models. Without some new physics, they have nothing to work with that they haven’t already had for 50 years, no new input that can tell them in which direction to look for the ultimate goal of unification and/or quantum gravity.
That the LHC hasn’t seen evidence for new physics is to me a clear signal that we’ve been doing something wrong, that our experience from constructing the standard model is no longer a promising direction to continue. We’ve maneuvered ourselves into a dead end by relying on aesthetic guidance to decide which experiments are the most promising. I hope that this latest null result will send a clear message that you can’t trust the judgement of scientists whose future funding depends on their continued optimism.
Things can only get better.
[This post previously appeared in a longer version on Starts With A Bang.]
I hope that particle physicists listen! For now, I hope most of them move to condensed matter physics, where the experiments are cheaper, you can make lots of different mini-universes with their own Lagrangians, and there are even practical benefits.ReplyDelete
Exactly, there are great works on these just to mention few Kitaev, Xiao-Gang Wen, Volovik etc. Condensed matter physics is the best direction and its very productiveDelete
you write: "What worries me much more is our failure to learn from failure."
Thanks, that is the best sentence I have read about particles physics. Though I am not much gifted with patience :).
Did I understand correctly? Do you mean that technically speaking, this dead end has no end?
Not sure what you mean with the dead end not having an end. I am not very optimistic anybody is actually going to listen to me in case that is what you mean.
Dear John and Sabine:ReplyDelete
Yes, we are now in a "little" nightmare, the big nightmare scenario will come if the LHC does not find nothing new at high luminosity (and it is sadly more likely than ever before)...The Big Desert could be true after all (something that I am sure some guys with asymptotically safe theories will enjoy).
Some theorists have already listened. You can see condensed matter papers in the arXiv written by or approached by stringers. It is not bad, but fundamental physics with colliders, unless something really new appear (and it is hard with the data at hand) is doomed. Even, I have seen lectures on black holes oriented from condensed matter physics.
I am sure Higgs physics will come, with high luminosity and precision tests at the ILC, the Great Collider and other, but the future of particle physics is placed at astronomy and astrophysics. Out there, we have particles beyond any collider we could build in the near future (unless a radical new tech were discovered of course, but I am not optimistic).
In my opinion, and I have explained this to many people in the las 5 years, the future of particle physics is to observe the high energy Universe. Tools are now being build or designed and it is much more efficient to do it so. The most promising tools for approaching quantum gravity is via neutrino oscillations (neutrino telescopes or neutrino experiments) and gravitational wave astronomy via interferometry. With complementary aid of the large interferometer arrays in Radioastronomy (or gravitational wave astronomy), with projects like the Event Horizon telescope or the GRAVITY instrument, we are very near to observe the black hole horizon of our galaxy and other radio sources.
I am not saying collider physics should be cut down...Or dark matter experiments...Only that they should try to refocus. It is a debate we will face soon. In less than a decade, dark matter ground detectors will touch down the floor where they will become sensitive to neutrinos coming from the sun, so in that respect, fundamental physics in the dark matter searches via indirect detection with nuclei is going to merge with another prediction yet to be tested: the neutrino-nuclei neutral coherent scattering, with a cross section proportional to the Fermi constant squared...
Said this, investing in colliders will be necessary...Maybe some day we will have a lunar base, a site where in addition to telescopes we could build new and bigger colliders...The collider physics on the Earth is much more limited than space based missions and projects. I have no hope to see in my timelife, but I wish I will see hints of Quantum Gravity looking at the Universe, perhaps it is the only way...Until a new genius appear and tell us what it the right theory of theories...
About the Great Collider in China, if the LHC is right and nothing but the Higgs is "close to us", we should perhaps focus on the muon collider. Less big but much cleaner to extract precision physics data we will need.
Finally, null results are the common ancestors of big revolutions. The Michelson-Morley experiment was done and we had to wait several decades before new big things come into physics.
P.S.: A hint of hope, in these dark ages, is that we only know the 5% of the Universe, to know and understand the remaining 95% is going to be the most fascinating and intricate adventure for us and the future physicists. I am sure we are not going to give up right now, are we?
I think you understand what I mean: Pushing susy (or another beauty) to higher energies forever...
I think you know where I stand w.r.t the SM and GR, but I'll state it: free parameters taken together are coherent and come from an underlying physics (pretty much like chemistry from particles physics); the thing we observe is not fundamental and the underlying "mathematization" can be reached by inference (maybe also by experiment but probably not in my lifetime).
Good article, Sabine, thanks.ReplyDelete
One thing to note, though: we are not quite yet at the nightmare scenario. The 12 fb-1 presented today is not even enough to completely saturate our parton luminosity of what was presented, and let's be clear: we have not even COMPLETED 80% of the searches with 2016 data (which was delivered *two weeks* ago).
After next year, the "lamppost" searches will be completed. Hopefully we find something. However, this is still not the end of the story if we find nothing. There are many searches that are not energy driven and could be hiding at lower masses, but would need lots of luminosity to tease out.
But to be clear: these are not even remotely "less natural", they are just harder to do. Not finding anything in the next year only means BSM physics will not be a quick discovery but a long slog, and we must have patience. I won't even begin to worry until next year.
There is a possiblity, Sabine, that the dark matter decays (or interacts) producing UV photons: http://iopscience.iop.org/article/10.1088/0004-637X/798/1/14ReplyDelete
Yes, I remember Dad used to worry quite a bit about a 'desert' in accelerator physics after the Higgs (unlike his great friend Julius Wess, who always felt that the first SUSY particle was just around the corner).ReplyDelete
The frustration is understandable from a theorist's point of view. However, I think the situation is a little different for the experimentalist. After all, it's reasonable to explore the next energy frontier and see what shows up, at least for a while. One mustn't forget that experimental physics works primarily by ruling things out, as my old supervisor used to say.
It's possible particle physics may find itself in the same situation as GR in the 40s and the 50s. We can't expect experiment to track theory faithfully, there will always be periods of drought while experiment catches up. And maybe it won't be such a bad thing if theoreticians and experimentalists focus more on other areas such as condensed matter physics. Many important breakthroughs were made there before, as you know.
However, my feeling is that the next big discoveries may come in observational cosmology - hopefully these will show the way for the next generation of particle physicists
"followed by a ritual parameter adjustment to explain the lack of detection" Defective postulates (SUSY) deliver defective predictions (proton decay). Procrustean observations only!ReplyDelete
1) Left-handed baryogenesis and Weak interaction. GR is only geometry. Test spacetime geometry with geometry, page 7 of the arXiv pdf, arXiv:1207.2442, doi:10.1088/0264-9381/29/18/184002 Enantiomorphic space groups P3(1)21 versus P3(2)21 single crystal alpha-quartz test masses.
2) LIGO observed 0.2 second to merger and equilibrium of 30 and 36 solar masses black holes (BHs). GR suffices. No unlimited redshift, no firewall, no quantum anomalies. BHs are 2D (with curvature) event horizons. Internal volume and singularity lack models for not existing.
"We’ve maneuvered ourselves into a dead end by relying on aesthetic guidance to decide which experiments are the most promising." Chemistry is empirical. Look.
"I’ve been laughed at when I explained that I don’t buy into naturalness because it’s a philosophical criterion, not a scientific one. But on that matter I got the last laugh: Nature, it turns out, doesn’t like to be told what’s presumably natural." - This is very important. Simplicity and esthetics indeed have no special reason to be efficient in physics. Maybe disappointing to some, but the data always comes first.ReplyDelete
we entered the nighmare scenario? Far from it, only the period of 'normal reality', when further progress at the LHC will rely on careful work, after the immediate fireworks predicted by the speculative bubble in particle theory failed to materializeReplyDelete
IMHO -- the future of physics lies in the definition of spacetime on a quantum level. Loop quantum gravity and that sort of thing. If I look at empty space, is there nothing there or are there "voxels" updating a null state?ReplyDelete
This may be a bit of a tangent, but - I do agree that Physicists have been throwing themselves at the same basic theoretical framework for decades, now. I want to run an idea by you - consider that there may be no such thing as Dark Matter or Energy. We did sort of just 'propose' it to explain the rate of expansion of the universe, after all. And then just got stuck on the idea, since then.ReplyDelete
I have an alternate explanation: that gravity and spatial expansion are *the same fundamental force.* And I'm going to try to keep this fairly short, but - basically - space expands in all directions by default (which we know to be true) but it does so proportional to the relative absence of mass nearby. With the presence of enough mass, spatial expansion actually reverses direction, and contracts - thus: gravity - as we currently observe and understand it. But given enough distance between objects, spacial expansion starts to take over, at a rate proportional to the distance between masses. Think of it as an 'inverse' to the effect of gravity, just on the opposite end of the same spectrum. Hence, planets orbiting a star will very, very slowly start inching away from the star (which they do). The further out a planet is, the faster it's drift. So, really, we're not exactly seeing an increase in distance per-se between heavenly bodies; we're seeing a tiny but noticeable increase in the amount of *empty space* generated between them - which of course can also be classically measured as 'distance.' The effect is just really small, because the relatively strong local gravitational fields keep spatial expansion to a scaled minimum, in that area. Same thing with galaxies, but on the opposite end of the scale: the truly VAST distances of empty void between galaxies keeps expanding at such a high rate because the force of spatial expansion is almost entirely unchecked. There is little gravitational influence to curb the expansion.
The nice thing is, this is all very easily testable.
very nice column. be optimist. remember: it's always darkest before it goes pitch black. :)
Back when I was taking nuclear and particle physics, in the 1980s, our prof noted there was then a fairly substantial population in the community who had nicknamed the Superconducting Supercollider (then being planned) the 'Desertron' because they expected it to be unable to reach, by some 15 orders of magnitude, energies required to go outside the standard model.ReplyDelete
This was considered a bad way to advertise for the scsc, and disloyal to the field. But, looks like they were right. Or at least more correct.
Time for a new paradigm to emerge from the crisis.ReplyDelete
Harder, better, faster, stronger ... collisions ... we can't stop, it is in our DNA to play with fire and keep on going, this is the zenith of a 100.000 year old human habit, smashing rocks together to build sharp weapons and lit fires, instinct.ReplyDelete
Rapo above: 'But to be clear: these are not even remotely "less natural", they are just harder to do'ReplyDelete
Also, we assume that evidence to date is incomplete. Often in science it is the incomplete observation and analysis evidence.
re:" I hope that this latest null result will send a clear message that you can’t trust the judgement of scientists whose future funding depends on their continued optimism."ReplyDelete
This American quote has been used in politics and business, now it's in science, and not only in HEP.
“It is difficult to get a man to understand something, when his salary depends on his not understanding it.”
I definitely like your description of the last 30 or so years as "The Dark Ages".ReplyDelete
A wonderful article, thank you!
Bee - Just as an FYI in case you do not know, you have a 280+ comment thread on Hacker News! (A few dolts seemed to think your post was clickbait, heaven forbid they actually read the post) As always, insightful comments though must say I refuse to go to any Forbes associated sites.ReplyDelete
I think you're being a little selfish and narrow. Physics has made so much progress in last 200 years that today we are on the verge of a theory of the whole universe. As the problems get bigger and the domain grander and more all encompassing, naturally progress slows down. On the scale of your career it may seem frustrating if the next big step forward takes 100 another years.. but on the scale of science / humankind, it's OK ..ReplyDelete
great summing up, sabine..condensed matter may be the direction career wise, but it will not beReplyDelete
particle physics, no matter how exciting the developments in it..
"our reliance on gauge-symmetry and the attempt at unification, the use of naturalness as guidance, and the trust in beauty and simplicity aren’t working."
Are there any alternative ideas which are floating around, say by "little people (!)"? Are you complaining that these alternate ideas are drowned out by the big crowd?
Thanks for letting me know, that explains the uptick in my stats. I hadn't really expected anybody to read this post who wouldn't know what the "nightmare scenario" is - that will teach me. In any case, it's like the old xkcd joke about putting a typo in the title ;)
Of course I am selfish. But you're mistaking my point. I can't tell you how fast progress can be, and certainly there must be a limit to human capacity. I can tell you however that we're not anywhere close to this limit because we're disregarding that investments are not made efficiently.
And we're not anywhere close to having a theory of the whole universe, sorry for the bad news.
yes, there is at least one alternative, by one (seemingly) "little people", which in my opinion is guided by naturalness and simplicity, not by gauge symmetry. As far as I can judge, it seems to work from A to Z; or if you prefer, from alpha to the Z boson and gravity, but it does not use (or even link) to gauge symmetry.
You may be right about the "big crowd", I don't know and I am not interested - they have been sterile for too long and a crowd often fools itself for centuries.
On August 4, 2016, in response to a pessimistic post on his article "A Flash in the Pan Flickers Out", Matt Strassler states: "The LHC has collected 2% of its data, and searches through the data are far from comprehensive".ReplyDelete
I assume this means that the LHC will continue running collisions at its current energy/intensity level for some time to come, until 50 times as much data becomes available for scrutiny. Perhaps there's still hope that something might still show up beyond the Standard Model.
The LHC has not only told us that the SM rules and everything beyond it (except gravity) sucks, but also that the Higgs mass balances exactly at the border of the stability region. 1 GeV less and the SM vacuum would be unstable, 2 GeV more and the SM would be boringly safe in the stable region. I think this is exciting, if nothing else because it is pretty much the only new theoretical principle that has come out of the LHC.ReplyDelete
Great post, I am wholeheartedly with you on naturalness. My hope is that "the failure of the LHC" will force us to be more creative with our next experiments - more IceCube-like or LUX-like. Cheaper, less model-dependent, and more discovery-oriented. I also hope we are willing to take seriously the idea that dark matter/dark energy might have some solutions outside of particle physics, from the mathematical or gravitational point of view. Gauge theory is really beautiful to me - but there are lots of other beautiful mathematics out there, like NCG or schemes, and recasting our theories in that language might lead to new ideas about the stuff we still don't know about.ReplyDelete
Always refreshing, thanks for sharing your perspective on this!
I'm a bit surprised by this post. The LHC has only produced a small fraction of the data it is set to deliver during its lifetime. A future LHC discovery of SUSY with, eg, gluino and stop masses larger than their current limits, would also be considered to have addressed naturalness.ReplyDelete
The problem IMO is one of sociology as much as science. Too many optimists, too much hype, some groupthink, and the lack of any breakthrough scientific result (comparable to, eg, W,Z discovery etc) over the past 40-50 years have distorted the scientific debate. Judgements on the extent of fine tuning needed to keep a theory natural are subjective. Yes the goal posts have been moved but they were fairly arbitrarily sited in the first place. We weren't in the nightmare scenario last week, nor are we there now. We may well end up there one day but there is a lot of data to be collected before we can we properly draw that conclusion.
I should add that I'm an experimentalist on one of the big LHC experiments. I'm no big fan of naturalness (is fine-tuning even a problem in a renormalisable theory since we place our energy cut-off where we want ?? ) but I can see that it could provide some motivation for expecting new physics. My prejudice is that our ideas of naturalness are wrong and so, in an odd way, I'm happy that the data are as they are right now. However, the data may say something very different next year. Its premature to draw too many conclusions about BSM physics from the LHC results today, just as it was premature (for many) to expect early discoveries.
Thank you for the post. I visited another web site by "he who must not be named"; the rampant racism, sexism is simply appalling. I made a small contribution to you to express my support and to just feel better.ReplyDelete
Wonderful post! I totally agree with your conclusions!Theorists must move to other directions of research and leave behind them the speculative failures of string theory's establishment, supersymmetry, multiverse e.t.c. Science needs desperately some fresh minds to replace the failed "revolutions" of the last 40 years with totally new ways of thinking! Thank you for your illuminating posts!ReplyDelete
So, is the hope of finding a graviton essentially dead? Are there any other proposed energy levels it could exist at?ReplyDelete
Is it possible other physics could be revealed at lower energy levels by colliding heavier atoms, like isotopes or various radioactive elements?
This is an excellent summary of how I see the situation - thanks, Sabine!ReplyDelete
The only thing you said that made me hesitate is "That the LHC hasn’t seen evidence for new physics is to me a clear signal that we’ve been doing something wrong, that our experience from constructing the standard model is no longer a promising direction to continue." But I've long felt that symmetry breaking and inter-generational mixing have not gotten nearly as much attention as the fermion and gauge sides of the standard model. With a couple exceptions (e.g., Technicolor) I've not seen very much investigation and imagination applied to where symmetry breaking/mixing comes from or how they can be generalized. The basic and mysterious Higgs mechanism has simply been taken over to BSM theories intact, with little change beyond the number of Higgs particles.
I have fantasies that someone will come up with a different approach to symmetry breaking that provides deep insight. If we're lucky, that insight would include explanations of multiple generations and mixing. I suppose you could say that this is beyond "our experience from constructing the standard model", but it would be an incremental building on our knowledge of the standard model rather than throwing the whole thing out and staring from scratch. In other words, it seems to me that there are still mysteries of the standard model that the standard model is telling us to explore.
Amazing article. I have a feeling that we have digressed from the original meaning of what is meant by "natural". What we think does not necessarily mean it is natural but only what is intuitive. The Universe as it is is already natural -- by its very nature -- and our model of this Universe necessarily need to respond to it by assimilating its presentation (experimental data/naturalistic observations/measurements) into the models we create.ReplyDelete
Models have to give way to data. Our minds have to give way to the physical reality.
Nature is not necessarily consistent with our intuition. This is one sentence that I can obtain from this beautiful narrative. Our intellectual guess must always start with available sense data. Otherwise, it remains a philosophy, not natural philosophy (a.k.a. "science").
However, I also believe that in so far as our data is limited, our intellect may dream of what could be natural in this Universe.
I have gotten a lot of comments to this post with links to your blogs or websites or vixra papers. I do not approve any such comments. If you have to say something, please avoid the links. Best,
Finally an educated opinion on the topic. Others have 'hangover' and the like ...ReplyDelete
But is it right to blame the failure on the naturalness argument being 'philosophical'?
I always thought that this motivation is overstretched and my impression was that it is rather a physicist's poor man's philosophy. Can naturalness be called a majority opinion of philosophers? At least the way in which it was handed round by physicists seems to hardly meet the degree of sophistication of a philosopher, even if we may not agree with their ideas.
For instance, I remember reading some philosophical papers that argued the opposite. The bottom line was that the fine-tuning problems may have occurred because, each theory being a combination of dynamical equations and parameters, we have constraint the dynamics a lot and therefore necessarily created tension among the parameters.
I am asking because my impression is that the phenomenological work in particle theory of past years followed a shotgun approach. It seems to me that this will hardly help to uncover a theory beyond the standard model, if it exists. Shouldn't we try to be more sophisticated in our motivations?
I think you misunderstood this comment. I didn't mean to say it's been justified by philosophers. I mean to say it's a non-mathematical argument that physicists have been using for unscientific reasons. Saying that it's philosophical is the nicest that came to mind. Maybe it would be more appropriate to call it aesthetic. But really all that matters is that it's not a mathematical argument. It's often excused as being based on experience, but it has a pretty lame track record, so that can't be it. Best,
Follow up question:ReplyDelete
I may over-interpret you again, but does this mean that only mathematical arguments should be used in the search for new theories? I think that the history of science would tell a different story there.
Perhaps you just mean to say that we relied to much on the naturalness argument, thinking that because it involves numbers it is very serious (mathematical). I'd agree with it.
No, I don't mean that only mathematical arguments should be used. I simply mean that one has to be aware what is and what isn't a hypothesis. Naturalness is a hypothesis, but it hasn't been treated as such. It has been used - and is still being used - to make predictions, despite its blatant failure. Why? Because physicists don't realize it's a hypothesis. At least that's my best explanation. Tell me a better one if you have one?
Yes, naturalness and finetuning are subjective. Yes, you could argue that maybe it's still natural now, with a 1% finetuning. And while we're at it, why not allow a 0.1% or 0.0001% finetuning? It's a combination of aesthetic bias and communal reinforcement. I think I agree with what you say. Best,
That's what I am thinking.ReplyDelete
Likely, there is also a sociological problem. @Summerisle mentioned that. The community has simply repeated the argument too often. People talked themselves into it. Solving the hierarchy problem became a standard argument that was valid without further need for justification. More, if they had really started to think about it, should have realized (some had realized). But the reward system we have does in my opinion not immediately support this independent thinking.
Excellent points! Even amateurs like myself can plainly see greater minds banging their colletive heads against the Wall. The physics community issues with cognitive dissonance.ReplyDelete
@cotster88 "greater minds banging their collective heads against the Wall" Reality is left-handed. Physics is mirror-symmetric. Don't theorize more, look differently.ReplyDelete
1) It is not a desired solution. 2) It lacks precedent . 3) It would have been proposed earlier if important. 4) It contradicts accepted theory.
PNAS 14(7) 544 (1928) Recanted
Phys. Rev. 104(1) 254 (1956) Unwanted
Phys. Rev. 105(4) 1413 (1957) Two pages; Nobel Prize/Physics
Phys. Rev. 105(4) 1415 (1957) It was trivial
Here's an interesting paper, mentioned at another blog, that uses 2015 data in the search for evidence of top squarks: https://arxiv.org/abs/1606.03903 Apparently there's some supporting evidence for a top squark and neutralino, though not sufficient to qualify as a discovery.ReplyDelete
Great article! I mostly agree with it while lively remembering discussions in the 90s with some of my profs who were totally convinced that LHC would, at the very least, discover SUSY. The possibility of that doesn't happening was just anathema to them.ReplyDelete
However, for the sake of the field, I still hope that LHC will come up with something unexpected.
Logically, it is entirely possible that physics will proceed to the point where it becomes physically impossible to decide between competing and logically inconsistent theories. That is, it may be that someday there will be two or more theories of physics that predict the results of all feasible experiments and observations, and yet these theories might not only be logically inconsistent, i.e. impossible to combine, but also might be based on different intuitions as to the ultimate nature of physical reality.ReplyDelete
Well now that actually sounds like the most feasible TOE I have ever heard on a science board. It could also be applied to the current religion/science debate, or politics for that matter. It would be kind of funny if physics and cosmology went down that rabbit hole!ReplyDelete
My guess, you could be most certainly right and our hyper complex abstractions have nothing to do with much except superficially Like astrology. Some would be offended by that, I didn't say is astrology, I said like astrology. We can split out Experience-visually see the star moves,. narrative-you will have a great day tomorrow!!! A narrative is still a narrative regardless of accuracy. Accuracy doesn't make it more than narrative. Like a photo is not more real than a stick figure.
A nightmare scenario? For who? Suppose CERN had discovered some new phenomena. Should it solve the big questions about the underlying reality of nature? Of course not. May be it is a nightmare for all those people who want the next particle accelerator. I hope so.ReplyDelete
Another wonderful post chez Sabine.ReplyDelete
It looks like the LHC is producing a result. It's just not the result we wanted. I still think the LHC is a valuable tool, but we need to start looking elsewhere.
This is an expanded version of what I posted on Facebook.
I am really disturbed that you would make the statement: "We’ve maneuvered ourselves into a dead end by relying on aesthetic guidance to decide which experiments are the most promising.". I think this does an enormous injustice to the way particle physics experiment has been planned and carried out in the past decades. It seems to me that to justify this claim, you should really explain which experiments you think particle physicists let go based on faulty prioritization. After all, if there isn't an obvious alternative that "languished because everyone lost their heads and built the LHC", it is hard to write what you did. There needs to be an alternative to the dead end that we failed to explore along the way, or no one can be blamed for our finding it.
I suspect you'll find if you inform yourself about how particle experiments have been planned, that your statement is very unfair to those who did the planning. Many very intelligent people have been trying hard to break the standard paradigms in creative ways for many years, and the governments of the world have been willing to invest in these efforts (maybe less than we want).
Ultimately, the LHC is a small (though important) part of that broader program. And unlike what you wrote here, it was not built to discover supersymmetry: it was built to illuminate the nature of electroweak symmetry breaking. It turns out so far (as several people have noted above) to be realized as the most boring possibility we could imagine: the vanilla Higgs mechanism. (And it may still turn out to be more complicated than that, though it looks like it at the ~10% level). But even if so, we have learned a lot about physics from this unqualified success that the LHC has already given us. To call it a dead end feels to me like the height of hubris.
There are truly unbelievable research happening in experimentation these days and yet science has predicted that these wonders must exist. I am referring to monopoles, tachyons, and micro black holes, quantum teleportation, hadronization, multi-particle entanglement, high temperature Bose Einstein Condensation, and non-associative quantum mechanics. These wonders have been searched for by science for decades. String theory and the theories of everything are based on the proposition that these wonders must exist. The string theorists have books filled with equations describing how these items must behave and yet when these behaviors are seen in experiment exactly as predicted, they say that these behaviors are impossible. What craziness!ReplyDelete
Yes it is embarrassing. CERN wants to build a meson factory to help in their Higgs boson research for the tune of 20 billion euros, but Leif Holmlid, a chemist is producing K-mesons and fusion using a green laser pointer, Deuterium and some catalysts. Now that is embarrassing. Mark LeClair can generate rare earths and even transuranic elements from water by using a metalized water crystal that he has produced. Just imagine what science can do when they understand what they have predicted to exist does in fact exist. Maybe they will discover Dark Matter and the cause of Dark Energy, maybe they will understand how eternal inflation works, there is the lithium mystery to uncover, and many other impossible cosmological observations to unravel that maybe made understandable in the context of the new condensed matter paradigm. There is a new world of science awaiting, it only requires the imagination to step through it.
Also an expanded version of what I posted on fb.
You know that argument that it can take a long time for a research program in hep-th to bear fruit? Well, that sword cuts both ways. It's ridiculous to complain (like you and others do) that there is a lack of big alternative research programs when there's no funding for those. Many intelligent people who have been trying hard to break the standard paradigms in creative ways.... left academia. And they still do.
I don't know which experiments went down the drain that way - nobody knows. That's the whole problem.
Sure, I know the LHC wasn't explicitly built to test SUSY. But if you're denying that particle physicists have long argued that the LHC should see something besides the higgs based on naturalness arguments you're either lying to yourself or to others. It's well documented in the literature and I can give you dozens of quotes from papers or seminar slides where people promote this argument. Now suddenly nobody wants to have said it.
I didn't say we shouldn't build a next collider, please don't put words into my mouth, I find this very tiresome. I'm saying if we do we should do it for the right reasons. I'm not against collider physics, that's totally not my point.
And some context for other readers: He's a particle physicist...
I always felt that "naturalness" is a consequence of theorists taking their perturbative techniques too seriously. I recall once reading (hearing?) Gordy Kane dicussing a "principle of perturbative stability" (or something to that effect) as though it was something really profound. I imagined Mother Nature having a good chuckle over that.ReplyDelete
If the LHC has not delivered the expectations, that is probably more useful for science. As Robert Pirsig wrote, the TV scientist who sighs "Our experiment is a failure; we didn't find what we were looking for." is suffering mainly from a bad script writer.ReplyDelete
So, great for the LHC. Not so great for those who "knew" what it would uncover.
Something of the opposite: the Hubble Space Telescope has director's discretionary time. Someone suggested pointing it somewhere which appeared to be blank and exposing for a long time, just to see if anything was there. The Hubble Deep Field and its successors have taught us a lot.
Maybe at the end of the day what you wrote is the most truthful. The Lack of respect of Mother nature is rather common.... Heraclitus wrote about 2,600 years ago, "the logos is common, but everyone seems to have their own private understanding", At about the same time in China Lao Tzu wrote, "whatever you say the Tao is, is not the Tao"....Same thing, and here we are 2,600 years later, still befuddled by these old statements as if they do not exist and the only thing that does exist and is the best is what ever is in our brains at the moment.....I know, I didn't write the above in mathematical symbolism, so it probably is difficult for "smart" folks to understand.
You say "I have gotten a lot of comments to this post with links to your blogs or websites or vixra papers. I do not approve any such comments. If you have to say something, please avoid the links."
One thing I've observed at events dealing with foundations (such as the last couple of workshops on emergent quantum mechanics) is that people are not much interested in each others' ideas. Forty people get up one after another and show slides with dozens of equations, and meanwhile the other 39 are all busy doing their email.
I agree that fundamental physics has been stuck for 40 years. But to break out of the cul-de-sac it's not enough for someone to have a bright idea. It's also necessary for there to be a forum in which novel ideas can be discussed. Right now, such a forum does not seem to exist.
Yes, maybe. But I hope you understand that I neither have the time nor the patience to provide that forum.
Spot on Sabine, you nailed it perfectly. Several pioneers of this approach even warned us that it didn't make sense (Feynman, Dirac). Witten's talk on "Living with infinities" seems to be the eulogy speech.ReplyDelete
I don't know what you mean. Dirac pretty much started this whole business with his "large number hypothesis". (Though Weyl came up with a similar thing slightly earlier.)
I think if we resolve some of the fundamental issues with QM, we it will set the tone for moving away from multiverses and anthropic landscapes. I like this approach and others similar to pilot wave theory:Delete
Much of this can be summed up with FAIRI DUSTReplyDelete
Frequent Ad hoc Interventions Repeatedly Invoked -in support of - Dubious and Unsustainable Scientific Theories,
I don't think "We’ve maneuvered ourselves into a dead end by relying on aesthetic guidance to decide which experiments are the most promising. I hope that this latest null result will send a clear message that you can’t trust the judgement of scientists whose future funding depends on their continued optimism."ReplyDelete
The decisions as to which experiments are most promising has more to do with technical feasibility than theoretical aesthetics. There is a vigorous program...including EDMs, CPT violation in neutral meson systems and other matter-antimatter systems, equivalence principle tests, searches for deviations from expected gravity at small distances or in response to the particle content of the test masses in the experiments, searches for time variations in fundamental constants, lepton flavor violation, various dark matter searches, etc. Experimentalists are entrepreneurial, and pay less attention to theoretical prejudice than you think.
If the experiment needs a billion or above, hope of seeing a signal is helpful. But both Gravity Probe B and AMS were funded at that level without much hope of a signal. *Experimental* aesthetics count... is the experiment well designed, clever, novel, nulling out systematic effects, etc.
Maybe those experiments haven't found anything shocking enough for you yet. If we give up trying to perform them, there will never be a shocking discovery, however.
"And yet we haven’t drawn any consequences from this: Particle physicists are still playing today by the same rules as in 1973."
"Without some new physics, they have nothing to work with that they haven’t already had for 50 years, no new input that can tell them in which direction to look for the ultimate goal of unification and/or quantum gravity. "
50 years ago (1966) quarks were not accepted. In 1973 was a year before the discovery of the charm quark, and 10 or so years before the discovery of the W and Z. It is really, really wrong to even imagine that experimentalists are bound by the same rules as in 1973... technology and sociology are very different now.
Perhaps the dates are nit-picking. But since 1974, the masses and mixing matrices of the quarks, leptons, and gauge bosons have been measured in a corpus of truly excellent experimental work. Although you say you've seen nothing but failure, I'd say both KAMLAND and Daya Bay/RENO succeeded during the time of your career.
A sad point is that the theoretical community has tended to give up on trying to describe most of those masses and mixing matrices from any deeper principal... atomic spectra did get explained in terms of a small number of fundamental parameters but for the most part, the fundamental fruits of the last 40-odd years of clever experimentation, that is, the actual values of masses & mixing matrix elements tend to be viewed by theorists as an accident. Maybe that is right, but maybe its a surrender to pessimism.
The theoretical community wants deeper insights and more shocking discoveries than mere parameter measurement. Actually, the experimental program I describe in the second paragraph does seek such discoveries, as would another collider beyond the LHC.
Or maybe the deeper insights and more shocking discoveries are already laying around in our existing data, unrecognized. Parity violation was first seen in 1928, as the wonderful essay by Luis Alvarez linked below details. Oddly enough, Alvarez' essay is from 1973, and he decried the influence of theorists on the experimental endeavor as you seem to.
I can't say there has been a lack of energetic, creative exploration on the part of experimentalists, only slightly held back by theorists. Alvarez was too pessimistic, and maybe you are too.
First, you're right that the "50" should have been a "40". Sorry about that.
Second, I did mention neutrino masses, see first paragraph. My point was that they were anticipated by theoreticians long ago.
Third, yes, experimentalists have their own agendas to push, but you're missing the larger context in which I'm writing this. As I have explained in much detail previously, the more difficult it becomes to test new theories the more careful we have to be when deciding what experiment to spend money on. And theoretical motivations certainly should play a role for that. The idea to just measure something because we can measure it will sooner or later fail in all areas of science simply because it becomes too costly.
Yes, sure there are experimental programs that look for this and that. But are they promising? Are they the most promising that we can do? I think they are most likely not, simply because the assessment isn't objective. I can only hope that maybe they're not entirely a waste of money.
Finally, I am very puzzled that you think theorists have given up trying to explain the particle masses and mixing matrices. In fact most of what they do is done for that purpose, on a very deep level, though maybe not explicitly. The whole idea of having a theory of everything or at least a grand unification goes there. Best,
On neutrino masses and mixings... as far as I know, that whole story is a complex interaction of experiment and theory, not, "anticipation by theoreticians". Ellis and Wooster, following up an a long back and forth with Lise Meitner, did the crucial experiment underpinning the existence of the neutrino in 1927, prior to Pauli; experimentalists were remarkably restrained in those days, and didn't claim a new particle. The old rule was... to claim a particle you need to measure its mass, lifetime, and spin.
Postulating a non-zero mass for the first neutrino is hardly a great insight... Fermi's Nuclear Physics notes from the 1940's show the impact of a non-zero mass on the continuous beta spectrum.
I think that the idea of more than one flavor of neutrinos was motivated by Steinberger & Lokanathan's experimental search reported in 1955 that the decay mu to e gamma had a very low branching ratio. A complex sequence of interactions between theoreticians G. Feinberg, S. Weinberg, Lee & Yang, and the experimentalists Schwartz, Lederman, and Steinberger ensued, resulting in the 1962 experiment for which the experimentalists received a Nobel. Flavor oscillations/mass differences seem to be from Pontecorvo, an experimentalist/entrepreneur, in the late 1960's... not the 1950's... although he seems to have written down neutrino/antineutrino oscillations in the 1950's.
Perhaps few discoveries in neutrino physics have resulted from the idea of "testing theories". Sometimes testing theories works... good examples include the positron, Z0, W, milliweak CP violation verified in the B0-B0bar system, the light Higgs. Maybe the top quark, but the theoretically predicted mass did wander up a huge amount between 1980 and 1995. Roughly an equal number of discoveries... the muon, parity violation, CP violation, the charm quark, the bottom quark, two neutrinos, neutrino oscillation... were not dominantly driven by the testing of theory. Serendipity and astute experimentalists perceiving new sensitivities arising from new technology are at least as important as theory in producing discovery.
The partial utility of "theory testing" in producing discoveries means to me... theory itself is not objective in its assessments. True objectivity means sometimes ignoring theoretical advice.
I do think the world's current experimental program is pretty darn good in its promise. "Most promising" can only be judged with hindsight. But I wouldn't ever characterize what is going on as "this and that". Every experiment underway has a terrific motivation of one sort or another... it is just that there is a complex "trading zone" of experimentalists, agencies, astrophysics, industry, theorists, etc that influences the priorities. It is and always will be messy, and I think that is probably a good thing. Were it totally clean and logical, I think the likelihood of a major mistake, like building the Maginot Line, might dominate.
As for the particle masses and mixing matrices... well, it is sort of self evident from your comment... "the rules haven't changed since 1973". During that time a very successful and challenging experimental program measured many masses and mixing matrices. The possibility that the actual numerical values measured might somehow be the game changer, the actual evidence of the deeper theory.... well if you thought that was a possibility you might say the need for new rules is obvious, and the main failure is that of theorists to discern the appropriate new rules.
One of my condensed matter colleagues here in Santa Barbara likes to say... Harry, if you start seeing superpartners, most particle theorists won't care. They'll call the mapping of the superpartner spectrum "mere spectroscopy, not fundamental". She has a point.... we've kind of lived with that attitude since 1973 already.
"Were it totally clean and logical, I think the likelihood of a major mistake, like building the Maginot Line, might dominate."
I never said anything about "clean and logical" - this is physics, not math, I know how much it's driven by intuition. I spoke about the need of it being objective. The problem I see that you either can't or don't want to see is that the way academia works today objective assessments are basically impossible. Scientists are more or less forced to do what's currently popular. And the ones who have funding are the ones who don't mind playing the game.
No, you can't judge "most promising" in hindsight, as you say, you have hindsight bias all upside down and might want to look up the word. In hindsight you'll only see whether what you did worked or didn't work and are likely to talk yourself into a story how awesomely great everything has worked. The way that you judge "most promising" is to enable the community to make the best possible judgements on where to spend their money. Of course that won't be perfect. Of course it'll be chaotic. But under the present circumstances it's almost certainly an extremely inefficient investment. Best,
Thanks Sabine... at least my experience is that on short time scales, subjectivity is important... we humans remain fallible, social, hierarchical creatures. Perhaps that is why the scientific method itself, with some idea about and striving for objectivity, was absent for most of human history. However, on longer time scales I think objective assessments do take over.ReplyDelete
Examples? No less than Ernico Fermi got a Nobel (about 1/2) for the discovery of the new elements Ausenium and Hesperium. He was wrong. Objectivity won in the long run. The UA1 discovered the top quark and supersymmetry in the 1980's. Even people inside the collaboration, subjected to a fair amount of bullying, dissented and objectivity won out in the long run.
I don't agree that scientists are forced to do what is popular. I'm aware of many experimentalists who pursue their ideas in defiance of the groupthink extent. And many figure out ways to get funded. Some theorists too, but I am less familiar there.
Hindsight bias is a nice idea, but contrarians do relish pointing out the dead ends and failures... the Materials Testing Accelerator, the Iron Ball, the original CLEO-I with azimuthally distinct detectors, the entire FNAL and DESY programs of fixed-target B physics. Maybe the Space Station. Maybe terminating the SSC. The neglect of much of neutrino physics.
You're right there is a tendency to mythologize the past... what I find more hopeful that that tendency is not absolute, just as the suppression of unpopular ideas is not absolute. Hope usually trickles forward... Ida Naddock was right about fission and is by no means forgotten.
Like all senior people, I've painfully experienced choices that went the wrong way... a few my own, many more of colleagues. But the years of hurly-burly even seem to me to be within a standard deviation or so of "best possible", factoring the errors that arise from the capriciousness of human nature. Luckily that capriciousness also drives some people to be stubborn, and marshall themselves through the disappointments.
Embarrassed to get Dr. Noddack's name wrong... should have checked.... Ida Noddack. And her paper from 1934 calling into question Fermi's conclusions is good, and was wrongly neglected... http://www.chemteam.info/Chem-History/Noddack-1934.htmlReplyDelete
A clear case where the promising work was overlooked.
Excellent article Sabine. Great to read from a truly objective scientist and not one seeking for next funding tap.ReplyDelete
I would respectfully suggest that the underlying ontology, i.e. physicalism, needs to be reviewed. No one really knows whether or not there is but one ontological realm. Should there actually be two or more ontological realms it could open up a whole new set of potential explanations for outstanding problems in philosophy and theoretical science.ReplyDelete