If my layperson's understanding is correct (probably vastly generalized), this should be considered exciting news. A few years ago the existence of the Higgs Boson was confirmed with some degree of confidence. These Higgs Bosons are produced when particles interact with the Higgs Field giving them mass.
The next question from that was - is that really the Higgs Boson, does it behave the way we expect it to (according to standard model)? I believe this is a test to verify that it does and they measured the coupling constant and it matched up. Neat. This could help with a much deeper understanding of why particles have mass.
ATLAS physicist here -- you're mostly right! The existence of a Higgs boson has been confirmed with extremely high confidence. And this news... it's exciting in the sense that it's an important result, but it's a bit of a damper on those of us who were hoping to discover new secrets about the universe.
Interestingly, the primary production mechanism for the Higgs boson at the LHC proceeds via the fusion of gluon particles from the colliding protons. This seems strange at first glance, since the Higgs interacts with particles proportionally to their mass, while the gluons are massless. In the standard model, there is a higher-order process wherein the gluons annihilate into a virtual "loop" of top quarks (which are very massive), which then "lend" their mass to produce the Higgs.
Because previous measurements have been consistent with the Standard Model prediction, we already had some evidence that the coupling to top quarks was nominal. However, there are other possible scenarios involving exotic physics that could mimic this production mechanism, which could imply the existence of new forces/particles, and that the Higgs boson does not couple to "normal" particles in the predicted fashion. Because of the nature of these heavy virtual loop processes, it turns out that it's pretty hard to distinguish between different such scenarios by examining the kinematic properties of the events. Hence, the main observable is the rate, and even that can be made to match a wide range of values with or without standard couplings, given a clever enough theory.
This recent result demonstrates directly that the Higgs boson does indeed couple to the top quark in a matter roughly consistent with the Standard Model expectation (the CMS measurement shows an upward fluctuation, indicating even stronger coupling than expected, although this is probably just a statistical fluctuation). Therefore, no fancy/exotic physics (such as string theory, strong gravity, etc) are required to explain the observed production of Higgs bosons so far at the LHC.
> The existence of a Higgs boson has been confirmed with extremely high confidence. And this news... it's exciting in the sense that it's an important result, but it's a bit of a damper on those of us who were hoping to discover new secrets about the universe.
There is a certain beauty in not only accepting that you might be wrong, but actively wanting to be wrong because that could be so much more interesting!
And a certain sadness in the disappointment some obviously have when they accept that the less interesting outcome is the one that they receive.
Well, it's a bit selfish really. It's a terribly interesting outcome as it is, but the particle physicists in the 70's and 80's got to have all the fun.
Sort of how the chemists in the 18th and 19th centuries got to have all the fun.
"I'll call it 'Aluminum.' No, wait! 'Aluminium!' Uh... ship that first print run of my book with the wrong spelling to North America. Nobody will notice!"
"I'll call it Potassium, because it's found in potash."
"That's not very creative."
"Fine, I'll call it Kalium and give it a symbol of K."
"Where'd you get Kalium from?"
"Well, it's very alkaline, you see. It's from potash, after all."
"That's still not very creative!"
"Fine. We'll call it Potassium, but give it a symbol of K. Happy now?"
Sure thing! In broad strokes, the most formal way (in our field's typically frequentist paradigm) to calculate confidence/significance is to build a robust statistical model for your entire experiment (including the random effect that various uncertainties, etc will have on the outcome), and then to randomly synthesize many many outcomes of your experiment with respect to a given hypothesis. The outcome of each "pseudoexperiment" is boiled down to a single number, known as a test-statistic, and this way we can generate a distribution of that test statistic that gives you an idea of the probability of any given outcome. Then, when we do the experiment for real and get a single outcome, we can evaluate the compatibility of that outcome with the distribution of possible outcomes sampled from the statistical model (e.g. by calculating a p-value). Generally the Profile Likelihood Ratio is chosen as the test statistic at LHC experiments.
This is possibly the most highly-cited statistics paper in our field:
https://arxiv.org/abs/1007.1727
It provides asymptotic formulae that allow us to estimate these p-values without having to simulate our experiment tens of thousands of times. But it also gives a nice overview of the different test statistics one might use.
"Practical Statistics for the LHC" is a much more complete and thorough introduction, but it's quite long and technical:
https://arxiv.org/abs/1503.07622
"Statistics for searches at the LHC":
https://arxiv.org/abs/1307.2487
Similar to the previous one, but maybe more words and less math. Perhaps one of these will resonate with you more than the others!
Lastly, here is a public note that was created jointly by the ATLAS and CMS collaborations prior to the Higgs boson discovery. Basically, we got together and came up with a consistent way to present new results from the LHC, and this note documents those protocols:
https://cds.cern.ch/record/1379837
>"Question number one would be: Did I or did I not establish a discovery?
Question number two would be: How well does my alternate model describe this discovery?" https://cds.cern.ch/record/1099994/files/p205.pdf
I don't see the purpose of question number 1, it seems totally spurious. All you need to care about is how well the various models explain the data.
EDIT:
For example, with the famous "sun's gravity bending starlight" example they compared the observations with predictions due to Newtonian gravity x with predictions due to Relativity 2x, there was no need to check for zero deflection since there was no theory predicting that. However, if some value (including zero) inconsistent with both was observed a new theory would need to be developed. Then that theory would need to be tested on some other phenomenon.
> I don't see the purpose of question number 1, it seems totally spurious. All you need to care about is how well the various models explain the data.
You don't just try to find the model that best fits the data and claim a discovery if this isn't your null hypothesis. Rather, the data needs to be far enough away from that predicted by your null hypothesis that it is highly improbable that you would find data at least that far from the prediction if the null were true.
For instance, in your example, if they had observed 1.8x, but the uncertainty on that were 0.8x, no discovery would be claimed despite the relativistic model explaining the data better than the non-relativistic model.
>"For instance, in your example, if they had observed 1.8x, but the uncertainty on that were 0.8x, no discovery would be claimed despite the relativistic model explaining the data better than the non-relativistic model."
The data is consistent with the predictions of both models in this case. If we want to distinguish between them we need to get more/cleaner data or different data to compare to different predictions. What is wrong with that?
>"You don't just try to find the model that best fits the data and claim a discovery if this isn't your null hypothesis."
This is not what I am suggesting to do, see above.
>"Rather, the data needs to be far enough away from that predicted by your null hypothesis that it is highly improbable that you would find data at least that far from the prediction if the null were true."
If I understand your question right, you're suggesting model A (the Standard Model, say) and model B (your own pet theory) should be evaluated on an equal footing.
In principle that's fair enough, but in practice, the Standard Model has already passed lots of tests -- it fits the results of many, many experiments -- so we already have a high confidence that it's correct (or rather, a very close approximation to the truth for all the experiments we're been able to try). So brand new model B does not start on an equal footing. The null hypothesis is "model A is correct".
If there's some new experimental result that does not fit with the Standard Model -- and this usually not a clear-cut thing, but a statistical estimate of likelihood -- but does fit model B, that's a useful new result. If the error bars are such that it fits both models, you stick with the tried and tested model A, unless B has some compelling new advantage (like being much simpler than the Standard Model, say) and it also fits all other existing experimental data.
In that case report: "these results are consistent with model A and model B, since model A has been studied much more so we will stick with that for now". There is no reason to include these additional (usually elaborate) steps.
Also model A may be something like "Standard Model w/o sterile neutrinos", while model B is "Standard model w/ sterile neutrinos". My understanding is these will be supported by all the same previous evidence.
And anyway, if you want to include prior info there is a principled method of doing so: Bayes' Rule. The method described here is indirect, obfuscated, qualitative, and open to all sorts of bias. In general it seems inferior in every which way, why has Bayes' Rule been rejected for this purpose?
Also model A may be something like "Standard Model w/o sterile neutrinos", while model B is "Standard model w/ sterile neutrinos". My understanding is these will be supported by all the same previous evidence.
In that specific case, no, a number of existing experiments appeared to confirm the "w/o sterile neutrinos" model, so it was assumed that was correct. Just one older experiment fit the "w/ sterile neutrinos" model; that has only recently been reproduced successfully, so now that model is back on the table. But it's still possible that it's just a measurement error.
And anyway, if you want to include prior info there is a principled method of doing so: Bayes' Rule. The method described here is indirect, obfuscated, qualitative, and open to all sorts of bias. In general it seems inferior in every which way, why has Bayes' Rule been rejected for this purpose?
Good question, I don't know! I wonder if some of the LHC people commenting here can talk about the reason for sticking with Frequentist over Bayesian statistics?
I suspect this gets into some pretty deep issues around the philosophy of science. Are we looking for the "correct" theory, or just successively better approximations to reality, or what? I don't think you can easily say "the Standard Model is incorrect" -- we know it's incomplete, hence incorrect, but it also fits experimental data incredibly well, so it must be a close approximation to some level of reality at the very least.
(edit to clarify: what I mean is, I'm not sure how you set a prior confidence on "is the Standard Model correct?" in a Bayesian sense, since we already know it's partially correct and partially incorrect.)
>"In that specific case, no, a number of existing experiments appeared to confirm the "w/o sterile neutrinos" model, so it was assumed that was correct. Just one older experiment fit the "w/ sterile neutrinos" model; that has only recently been reproduced successfully, so now that model is back on the table. But it's still possible that it's just a measurement error."
I was talking about all the other types of observations used to support the standard model. Afaik the existence of sterile neutrinos would not change the predictions.
>"Good question, I don't know! I wonder if some of the LHC people commenting here can talk about the reason for sticking with Frequentist over Bayesian statistics?"
However, it is put forward that prior information should be involved in interpreting the results of the significance test. This idea has been rejected by all the giants and founders of modern stats (Fisher, Neyman, Pearson, etc). Its just some ad hoc thing come up with by stats 101 authors.
>"I suspect this gets into some pretty deep issues around the philosophy of science. Are we looking for the "correct" theory, or just successively better approximations to reality, or what?"
We're supposed to be comparing the predictions derived from our theories/models to data collected after the prediction was made and use these predictions to come up with useful tech and perform amazing feats.
>"I'm not sure how you set a prior confidence on "is the Standard Model correct?" in a Bayesian sense, since we already know it's partially correct and partially incorrect.)"
The current solution seems to be performing an elaborate ritual that obscures the true method of using collective opinion.
The method described is the extremely standard Hypothesis Testing method. The null hypothesis is that there is no new physics, while the alternative is that there is some new physics. The only difference is that in particle physics the standard isn't p < 0.05 but a 5σ significance.
For instance, the Higgs is part of the Standard Model but for the Higgs discovery the null hypothesis was that the Higgs does not exist.
>"The method described is the extremely standard Hypothesis Testing method....The only difference is that in particle physics the standard isn't p < 0.05 but a 5σ significance."
Yes, I know. This isn't at all a positive thing as you seem to think...
A more stringent significance level just means it costs more money or the data is much cheaper to collect. You can look up "NHST controversy", "NHST pseudoscience", etc to find many people discussing the problems for over 50 years. Here is a decent start:
https://www.lesswrong.com/posts/ttvnPRTxFyru9Hh2H/against-nh...
I've been lately seeing that this practice is infecting particle physics, which is not a good sign. I do not think they are overwhelmed yet though. Here is how it has gone in every field so far (education research, psychology, medicine, etc):
Eventually the field will stop caring about all actual quantitative predictions (some barely funded crackpots on the edges will publish in ignored journals) and researchers will only test a "null hypothesis" that everyone knows is wrong (eg, in the physics case a world where the standard model is assumed true but has no higgs boson). Then upon rejecting the (known to be false) null hypothesis, they will conclude some theory only capable of vague/malleable predictions is correct.
The way it works is simple, the null model acts as a strawman. The confidence in rejecting the null model is somehow translated into support for the researcher's favorite theory. How does changing the significance level address this problem?
> The confidence in rejecting the null model is somehow translated into support for the researcher's favorite theory. How does changing the significance level address this problem?
Not just any old favorite theory. For instance, an excess at a mass of 125 GeV doesn't provide any evidence for a new particle at 2 TeV. It does however provide evidence for a new particle at 125 GeV.
> Eventually the field will stop caring about all actual quantitative predictions (some barely funded crackpots on the edges will publish in ignored journals) and researchers will only test a "null hypothesis" that everyone knows is wrong (eg, in the physics case a world where the standard model is assumed true but has no higgs boson). Then upon rejecting the (known to be false) null hypothesis, they will conclude some theory only capable of vague/malleable predictions is correct.
If that were the case, we would have made a lot more discoveries by now.
>"If that were the case, we would have made a lot more discoveries by now."
In physics you still have quantitative predictions done in addition to checking the null hypothesis (which I why I said that was superfluous), if NHST adoption continues these will slowly be deprecated and replaced by only checking the null hypothesis. Seriously go read some old psychology before NHST destroyed it, they were developing quantitative theories of learning and everything [1,2]. Then go look at it now (statistically significant this and that with basically no progress for 60 years...).
Also, the significance level, constraints on p-hacking, etc are adjusted so that discoveries occur at the "right" rate. I'm not sure what triggered he move to 5 sigma in physics but it was probably something like "this seems too easy" so people started carefully double checking and getting conflicting results.
At 5σ, you lose a lot of the downsides of standard p < 0.05 hypothesis testing because the p value is so low.
Nevertheless, I suppose what you would suggest is just setting limits to start with and looking for a bump there instead. That's not a bad idea, and some (Gross, e.g.) have suggested setting limits even in discovery papers.
>"At 5σ, you lose a lot of the downsides of standard p < 0.05 hypothesis testing because the p value is so low."
I don't see how this addresses any of the issues, it just makes it more expensive (ceteris paribus). As I already wrote:
"A more stringent significance level just means it costs more money or the data is much cheaper to collect. ...The way it works is simple, the null model acts as a strawman. The confidence in rejecting the null model is somehow translated into support for the researcher's favorite theory. How does changing the significance level address this problem?"
>"Nevertheless, I suppose what you would suggest is just setting limits to start with and looking for a bump there instead."
Exactly, and the more precise the limits, the more meaningful for the theory if its consistent with the data. At the extreme, theories that allow for any value at all (as I understand the case is for every possible observation under string theory) are not supported by the data no matter how it turns out.
A more stringent significance standard doesn't just make it more expensive, since if what you're seeing is a statistical fluctuating, it will most probably disappear upon collecting more data, not get stronger.
Confidence in rejecting the null isn't "somehow translated into support for the researchers' favorite theory", it's translated into support for the existence of a signal, which makes sense since the null is the background-only hypothesis.
After we establish rudimentary support for a model by finding one or more such signals, we can then embark on the process of doing precision measurement to really test that model (as is being done for the SM).
>"A more stringent significance standard doesn't just make it more expensive, since if what you're seeing is a statistical fluctuating, it will most probably disappear upon collecting more data, not get stronger."
If its only a statistical fluctuation, the p-value due to sequential sampling follows a markov process (random walk) between zero and one (there is no convergence). So starting from a significant result, the p-value would be just as likely to decrease and become "more significant" as increase and "lose significance". The significance cutoff is irrelevant to this behavior, although the random walk will spend less time in these extreme regions to begin with.
Here is an example of the random walk in R. It was my first attempt when going up to 100k samples, after n = 45 the p-value was ~5e-4 (~3.3 sigma), later at n = 36441 it went even more extreme in the other direction, corresponding to a p-value of ~1.9e-6 (~4.65 sigma). Here is the plot and code: https://image.ibb.co/hOHO08/p_markov_chain.png
set.seed(1234)
n = 1e5
a = rnorm(n)
b = rnorm(n)
p = sapply(10:length(a), function(i) t.test(a[1:i], b[1:i])$p.value)
plot(p, type = "l", panel.first = grid())
> min(p)
[1] 0.0005394751
> 1 -max(p)
[1] 1.908121e-06
Perhaps I'm wrong and if you run enough of these and subset to only look after a certain threshold has been breached (ie 5e-2 or 3e-7) there will be different behavior, I doubt it though. However, that is all unimportant since it is based on a false premise:
>"_if_ what you're seeing is a statistical fluctuating"
You aren't you are seeing that, so everything that follows is irrelevant. The background model is imperfect (eg nobody believes in a standard model with no higgs boson, everyone knows it is wrong somehow). In this (realistic) case convergence to statistical significance is guaranteed with enough data. However, in the rare (non-existent?) case where the background model is thought to be perfect, it is a different story.
>"Confidence in rejecting the null isn't "somehow translated into support for the researchers' favorite theory", it's translated into support for the existence of a signal, which makes sense since the null is the background-only hypothesis."
This amounts to claiming that in most peoples minds (including the authors of the paper) the Higgs boson, gravitational waves, etc haven't been "detected with 5 sigma confidence"... How much would you want to bet on this? The null model could be rejected due to a loose cable (ftl neutrinos), but the p-value doesn't distinguish between these explanations. Perhaps there was "a loose cable" in the LHC experiments but nobody looked very hard since the deviation agreed with preconceived notions? The p-value doesn't help you here.
>"After we establish rudimentary support for a model by finding one or more such signals, we can then embark on the process of doing precision measurement to really test that model (as is being done for the SM)."
Why not just skip the first step? Instead collect data to check whatever models that exist. When none of them can explain it, modify or come up with new models until it fits. Then derive new predictions from those and collect new data to check them, repeat.
If what you're seeing isn't a statistical fluctuation, then you've found something, so it's right to claim a discovery. The point of hypothesis testing is to distinguish statistical fluctuations from real signals.
If you collect, say, 1000 samples of a normally distributed variable and find that the mean (for instance) is 2 sigma from the expected mean, then if you collect another 1000 samples and take the mean of all 2000 samples, you will probably find that the significance decreases, assuming the first result was a statistical fluctuation. This is just [regression to the mean](https://en.wikipedia.org/wiki/Regression_toward_the_mean).
What we don't do is dishonestly drip-feed data until we hit the significance we want, then stop. Data is added in fairly large chunks (generally an year's run at a time), and when a new dataset is added the analysis is developed with (at least the new) data blinded. The dataset is only unblinded when the analysis has been finalized.
>"If what you're seeing isn't a statistical fluctuation, then you've found something,"
You have found a deviation from your null model. That is it.
>"so it's right to claim a discovery."
No, if you knew the null model was flawed to begin with nothing has been learned. Also I wouldn't refer to something like "equipment was malfunctioning" as a discovery. Drawing any conclusions about the actual research hypothesis must be done outside the NHST framework, or else there is a fallacy at play (probably strawman).
>"What we don't do is dishonestly drip-feed data until we hit the significance we want, then stop. Data is added in fairly large chunks (generally an year's run at a time), and when a new dataset is added the analysis is developed with (at least the new) data blinded. The dataset is only unblinded when the analysis has been finalized."
Great, but even if you don't p-hack it still doesn't work unless it really makes sense to assume the null/background model is perfectly true. P-hacking is just more BS on top of an already BS procedure.
In summary: If there is anything wrong with the null/background model at all, the p-value will converge on zero, it is just a matter of collecting enough data. This will happen regardless of whether the theory of interest (research hypothesis) is accurate or not.
> No, if you knew the null model was flawed to begin with nothing has been learned.
We don't know that the null is flawed to begin with. Not in a way that matters to the analysis anyway, otherwise you've picked the wrong null. No one runs analyses to discover the pion for the millionth time.
For BSM work, the way it generally works is this (ignoring limit setting):
- Pick a signature predicted by one or more BSM models (or even none), that either isn't predicted by the SM or is exceedingly rare in the SM. For example, you might predict a new particle that decays in some predetermined way.
- Define a signal region in some combination of variables where you expect to find a signal corresponding to this signature. This region is blinded, and you don't look at it until after fixing your entire procedure.
- Estimate the background in this signal region with a combination of Monte Carlo simulations and extrapolation from outside this region (data-driven backgrounds). This obviously has both statistical and systematic uncertainties, and a lot of the hard work is in getting this right. For instance, you might use independent Monte Carlo generators, or define control regions to check your estimation in.
- "Open the box" and look at the signal region data. If you see an excess over the estimated background, calculate the significance. Even here, if you were looking for a new particle, for instance, and the excess isn't a localized bump, this would be an indication that the background estimation may be flawed.
- If the significance is over 5 sigma, you have a discovery.
As you can see, you aren't using a null hypothesis that you already know is flawed. Your null is specifically "no signal exists". A positive deviation that isn't a statistical fluctuation is by definition a discovery of a signal.
Things like malfunctioning equipment go into the uncertainties if they occur in a way that the researchers have considered (which often means uncertainties are set conservatively if the equipment behaviour is poorly understood). If they occur in a way that no one considered, there's no statistical trickery that's every going to compensate for that. If we just went straight to setting limits, we would still see a deviation from what's expected there if equipment malfunctioned in a manner that faked a signal.
> In summary: If there is anything wrong with the null/background model at all, the p-value will converge on zero, it is just a matter of collecting enough data.
In summary: Assuming the background estimation is correct, the p-value will only converge to zero if a true signal exists. If the background estimation is wrong, then the background estimation is wrong and this is a problem with the background estimation, not hypothesis testing.
I'm by no means claiming the system is perfect, but it isn't systematically flawed the way you seem to be claiming.
>"Assuming the background estimation is correct, the p-value will only converge to zero if a true signal exists."
Aren't you assuming the background model is correct and a true signal exists?
>"Your null is specifically "no signal exists"."
No, it is never this. It is an entire model, one assumption of which is "no signal exists". The p-value doesn't care which assumption is wrong, it is only wishful thinking that leads to people focusing on that one.
>"We don't know that the null is flawed to begin with."
Sorry, I don't believe this. Give a concrete example. Do you believe the standard model is 100% correct? If not, then any background derived from it must be assumed to be flawed to begin with.
>"Things like malfunctioning equipment go into the uncertainties if they occur in a way that the researchers have considered (which often means uncertainties are set conservatively if the equipment behaviour is poorly understood). If they occur in a way that no one considered, there's no statistical trickery that's every going to compensate for that."
Correct, there is no statistical trickery to compensate for this. It is a scientific problem, not statistical.
Did you check out that Meehl paper I linked elsewhere?[1] If you take a prediction of a model and test that, messing up the experiment means you get results that diverge from your prediction. If you reverse the logic of science so that you test the "opposite" of your prediction, messing up the experiment yields results that seem to support your model. This is why the prediction of the theory needs to be set as the "hypothesis to be nullified".
1. If you're using a data driven background, you're background model isn't the Standard Model but that there isn't something special about your signal region.
2. If you are using the SM as your background, then yes you do believe it to be 100% true, since what you are looking for is evidence that there exists new physics not described by the SM.
In other words, the theory under test is the SM, and it can pass very easily. If it fails despite this, that's evidence that it's incomplete. If it passes, the limit setting stage tests whatever new physics we were looking for, and gives an upper bound on how sure we are that it does not exist.
> "1. If you're using a data driven background, you're background model isn't the Standard Model but that there isn't something special about your signal region."
Sure, it means you assume that during the signal detection everything was working exactly as it was during background data collection. There are going to be other implementation specific assumptions like what thresholds to use regarding environment noise triggers, accounting for sensor drift, etc. These data-driven models are approximations, I doubt the people actually coming up with them really believe they are 100% true. If you give a real life example I will point out exactly where there are issues.
> "If you are using the SM as your background, then yes you do believe it to be 100% true"
I don't know what this is supposed to mean. Of course you are assuming your background is 100% true. Do particle physicists actually believe this though? Not from my reading:
Yes, I already said the background estimation can be wrong. We can check it by defining validation regions outside the signal region and making sure it correctly describes the data there (where there is no signal) and assign a conservative systematic uncertainty to cover any differences, but yes it can be wrong. This is a background estimation problem though, not a flaw with hypothesis testing. By the way, the signal region data and background data are collected simultaneously, so there can be no systematic difference in experiment conditions between the two.
As for the SM, we are looking for those places where it is incomplete, and to do this we must assume it is complete and look for strong evidence that we are wrong. To date, it doesn't seem like we see though, as far as collider physics is concerned.
You know what's also a straw man? Not assuming good faith in a discussion and obtusely attacking something that isn't actually being done. You've been corrected two times now that the statistical testing methods you've been attacking are in fact not how the experiments are being done and that the choice of null hypothesis that you've been attacking is not at all the null hypothesis that is being tested against.
I know you're feeling very right and vindictive but damn if this isn't tiring to read. Make sure you know what you're right about first before assuming the other thing is wrong just because it matches a few keywords that you've read are bad. Because assuming good faith means that you allow for the possibility they might not be doing it wrong. You still get to make your point but it saves your face a lot.
I'd suggest, go outside, attack a windmill for a few hours, think about what you're actually trying to say, and if it's not "hey I read this article on lesswrong and it says everybody is doin it wrong", you'll probably find you can make your point much clearer.
You seem to have more than sufficient knowledge about statistics to think for yourself on this matter.
>'You've been corrected two times now that the statistical testing methods you've been attacking are in fact not how the experiments are being done and that the choice of null hypothesis that you've been attacking is not at all the null hypothesis that is being tested against."
Quote this. Where? I am sure by "corrected" you mean "someone claimed something I believe to be wrong, so I continued to point out why." Amazingly, this looks like yet more strawman arguing...
Nice, really nice, introduction to statistical hypothesis testing, nicer, sorry 'bout that, than is common in teaching of statistics. Nice work by physics.
Some unusual clarity on how hypothesis testing works or should work.
For one more point, we pick the null hypothesis so that we can when we collect data we can calculate probabilities of that data assuming the null hypothesis is true. So, what null hypotheses we can consider are both enabled and constrained by the assumptions to calculate the probabilities given the data.
>"we pick the null hypothesis so that we can when we collect data we can calculate probabilities of that data assuming the null hypothesis is true."
That is an awful reason to choose a null hypothesis. You should choose a null hypothesis you derived from your theory so you can see if your theory is capable of making accurate predictions.
Yep, that's the "switcheroo" that reverses the long successful logic of science. I'd suggest starting with Meehl 1967:
>"In the physical sciences, the usual result of an improvement in experimental design, instrumentation, or numerical mass of data, is to increase the difficulty of the “observational hurdle” which the physical theory of interest must successfully surmount; whereas, in psychology and some of the allied behavior sciences, the usual effect of such improvement in experimental precision is to provide an easier hurdle for the theory to surmount."
But if you didn't do that, you would be assuming any crazy theory you think of is true, and require overwhelming evidence to refute it.
> I'd suggest starting with Meehl 1967
Your very quote states that this whole idea works for physics, and is describing that it doesn't work in psychology and social sciences. I'm confused by this:
To take the IQ example, if you take the set of all people in a country, for instance, and randomly select two sets of 5 people, you will find that their average IQ differs by some amount. If you instead select two sets of 50000 people, the average IQs should be a lot closer (to each other, and to the true average). This is by definition true, since IQ is by definition normally distributed. If that's not what you see, you have a methodological problem.
By "physics" he clearly is referring to testing the quantitative predictions of models. The first sentence of the abstract:
>"Because physical theories typically predict numerical values, an improvement in ex-perimental precision reduces the tolerance range and hence increases corroborability."
I don't know the historical details but it would appear that since 1967 the NHST virus has proceeded to begin its infestation of physics. Now physicists are acting more and more like psychologists (focusing on testing a null model rather than the predictions of their models; which is the first phase of the illness) and will reap the same consequences of stagnation, etc. Lowering the threshold to 3e-7 instead of 5e-2 just makes this slower and more expensive.
>"To take the IQ example, if you take the set of all people in a country, for instance, and randomly select two sets of 5 people, you will find that their average IQ differs by some amount. If you instead select two sets of 50000 people, the average IQs should be a lot closer (to each other, and to the true average). This is by definition true, since IQ is by definition normally distributed. If that's not what you see, you have a methodological problem."
I'm not sure why you are talking about standard errors of random samples from a population... He was just giving stats 101 background for philosophers so he could get to this point:
"While no competent psychologist is unaware of this obvious distinction between a substantive psychological theory T and a statistical hypothesis H implied by it, in practice there is a tendency to conflate the substan- tive theory with the statistical hypothesis, thereby illicitly conferring upon T some-what the same degree of support given H by a successful refutation of the null hypothesis. Hence the investigator, upon finding an observed difference which has an extremely small probability of occurring on the null hypothesis, gleefully records the tiny probability number “p < .001,” and there is a tendency to feel that the extreme smallness of this probability of a Type I error is somehow transferable to a small probability of “making a theoretical mistake.”
I mentioned the IQ stuff because I found it to be a strange example. By definition of IQ, it shouldn't exhibit any issues so long as the random sampling is done correctly.
In addition, there's a difference between saying "p is low so it is unlikely that the null is true" which is absolutely correct, and "1 - p is the probability the alternative hypothesis is correct". Certainly in physics people don't believe the second, I don't know about social sciences.
You are at least partly correct. My statement was correct, but it was intended only as an explanation of some of the mechanics of the applied math and applied probability of getting a doable hypothesis test.
The role of the test in a scientific theory was deeper than my statement!
In the main, novel hypothesis test I invented and published, there was more than just what I outlined and you criticized, more along the lines you mentioned: That "more" was something like "if the next observation is a long way from anything we've seen before, then maybe it is an anomaly?". The actual work of the math in the paper showed, intuitively, what "a long way" meant and, in particular, for the math, how actually to calculate, along the lines of my statement, the hypothesis test false alarm rate. So, in short, in nearest neighbors anomaly detection, with meager assumptions, we actually can calculate false alarm rate and, thus, get an hypothesis test.
And, then, we are not limited strictly to the single nearest but can do some weighted sum over several of the relatively near. Right, such things appear to be necessarily close to multi-variate probability density estimation. But such estimation commonly requires so much data that it is not a good, direct way to calculate or estimate probabilities; curiously we can do well with the calculations without actually getting a local density estimate although in a sense we are close to doing that.
The other remarks here are even better, e.g., get to how to do science, maybe at the LHC or some such. Good and beyond what I tried to say.
Really nice outline of part of the scientific method, much nicer than I was ever taught in science or physics classes. Physics has done well here! Hmm, borrow this method for some other parts of science ....
having you here i'd like to take the opportunity and to ask about tetraquarks.
if i recall correctly there have been several identified tetraquark particles over past years (many of detections coming from LHC) with hint of possibility of pentaquark.
i always wondered how does standard model includes/describes these?
Good question! That kind of stuff is a bit out of my area of expertise, but I have asked around my colleagues at CERN and various Unis with more or less the same question.
As far as I know, there's nothing too exotic (from a theoretical perspective), about tetra/pentaquarks. They are just QCD bound states of more than 3 quarks. The problem with QCD is that it's a non-perturbative theory, so we generally can't even do a good job computing the hadronic bound states that we already know exist!
So, I get the impression that these observations are mostly of interest to people doing QCD on the lattice (or other calculational methods), as inputs to their modeling. I.e. perhaps having an "answer key" for some tetraquark masses will allow them to better determine whether they should be modeling these states as bound states of two mesons (which each have 2 quarks), or as a totally different 4-quark structure.
> the gluons annihilate into a virtual "loop" of top quarks (which are very massive), which then "lend" their mass to produce the Higgs.
Why are the words "loop" and "lend" in quotation marks? Are they just a handy visual a lay person would understand to describe a more complicated phenomenon? Is there no better word to describe what is happening, including within your field, but it isn't a technically accurate description?
I'm envisioning a room full of highly educated folk excitedly talking over each other... "Well it looks like a ring, but it doesn't quite meet up..." "It looks like a disc, but with more 'weight' to it..." "No, it looks like a loop-the-loop on a roller coaster!"
In quantum field theory, perturbative physical processes can be expressed as the sum of all possible diagrams compatible with the initial and final state of interest. Each diagram corresponds to an integral, and diagrams that have loops are special because they are underconstrained by the initial/final conditions. Hence, you are left with an additional integral over every possible combination of momenta that can be exchanged within the loop. These integrals are usually hard or impossible to compute and may require weird mathematical techniques (like dimensional regularization). So, yes, (theoretical) particle physicists talk about loops a lot!
"Lend" here is total b.s. that I made up. The point is that the gluons can't directly interact with the Higgs boson, so they use their collisional energy to create some massive top quarks that can.
So a little from column A, a little from column B. Got it!
In all seriousness, I'm just interested in how much is being obscured when folk like Cox do a TV show, obviously written for those interested but not involved like myself. I've no idea what anything in your paragraph meant past the word "In" (yes, the first word), but I can definitely picture a loop, and get that there is a something which is transmitted / moves / traded / otherwise-not-at-its-origin within that loop, and trying to understand what that something is will leave me drooling into the carpet.
While you're explaining individual words here (!) can you help me understand that use of "virtual" in high energy physics?
"Virtual particles" implies they're somehow not real, but I assume the theory says they do have a real physical existence in some sense -- they have an influence on the real particles. Are they "virtual" just because they're extremely hard to isolate, so all our practical experiments are indirect, or are they different in principle from the normal, "real" particles that our experiments work with? Is it a qualitative or just a quantitative difference?
It’s been a long time (and this was never my strongest area), but in case someone who really knows what they’re talking about doesn’t get back to you, it’s basically a particle who may or may not exist based on quantum uncertainty, but in practice IIUC it’s more like an excitation of the underlying quantum field.
Both real and virtual "versions" of a type of particles are described as excitations of the same quantum field; the difference is that only the real particles can be detected experimentally, whereas the virtual ones are used to model interactions between (real) particles and thus only appear in calculations.
Would it be roughly correct to say that virtual particles by definition always vanish (mutually annihilate, etc, whatever) before the measured outcome of an experiment, therefore they definitely cannot be directly observed? But they're an integral part of the model, therefore if the model is correct, they really do have a real physical existence (in some complex quantum sense)?
I do not believe so. Generally speaking, mathematical models often include what I call "scaffolding," which is something that, while being part of the model, does not represent anything real. (Different models are likely have different scaffolding, and some future theory might do away with virtual particles as a mechanism of interaction.)
As I understand it, ’virtual’ particles are those that are not observed ”on shell” (i.e. going into or coming out of a specific interaction), and hence whose existence cannot be affirmed if not by the effect their evanescente presence had upon what did actually come out, or rather, the statistics of what comes out of many identical inputs interacting.
If anyone's looking for a really solid "accessible to a layperson but you're still going to have to put in some work" series on this stuff, I wholeheartedly recommend PBS Space Time on YouTube. It's paced like your standard 10-15 minute light educational fare, but the core is serious physics.
An excerpt from part 5, "The Secrets of Feynman Diagrams":
The overall interaction described by a set of Feynman diagrams is defined by the particles going in and the particles going out. These are the particles that we actually measure. We know their properties - for example, their energy and momentum. And they obey Einstein's mass-energy equation. We say that these particles are on the mass shell, or just on shell. They sit on the shell structure you get when you plot Einstein's equation of energy, momentum, and mass. On the other hand, everything that happens between the ingoing and outgoing tracks has questionable reality.
Each possible diagram that results in the same ingoing and outgoing particles is a valid part of the possibility space for that interaction. The particles that have their entire existence between vertices within the diagram but don't enter or leave are called virtual particles. Their correspondence to anything resembling real particles is debatable. They are also, by definition, unmeasurable. Otherwise, they'd be one of our ingoing or going particles. These particles do not obey mass-energy equivalence. So they are off shell. These particles aren't even limited by the speed of light or the direction of time, which leads to all sorts of fun.
Is there any way to describe the scale of these particles relative to those I learned about in high school chemistry (proton/neutron/etc)? Is that even a sensible question?
Totally sensible, and it's actually probably the easiest way for me to think about it as well :)
A proton or neutron has a mass of approximately 1 GeV/c^2.
The Higgs boson has a mass of about 125 GeV/c^2 -- so it's totally appropriate to think about it as being 125x heavier than a proton, or about as heavy as an Iodine nucleus.
The top quark has a mass of 170 GeV/c^2 -- it's the most massive fundamental particle we've discovered so far!
So I have another silly non-physicist question at this point: if Higgs is what gives particles mass, and it has a mass of 125 GeV/c^2, why doesn't this imply mass can only be conferred in units of this amount? We obviously have smaller particles with "real" masses (e.g. nuclei lighter than iodine). Is it that the Higgs is coupled by a varying degree which confers only part of its mass to the coupled particle? In that case, can a single Higgs be lightly-coupled to several distinct particles? Does this imply some other spooky connections/behaviors between multiple particles sharing partial couplings to a single Higgs?
Roughly, you can actually think of the mass of these fundamental particles being _defined_ by how much they interact with the Higgs field. Higgs bosons themselves interact with the Higgs field, to an extent that their mass comes out to be ~125 GeV/c^2. Tau leptons interact with it less, so their mass is 1.7 GeV/c^2. The key point is that the strength of the interaction of any given particle type with the Higgs field is a totally arbitrary, free parameter of the theory that we only know by measuring those particles (with the exception of electroweak bosons, which have a constrained relationship with the Higgs due to electroweak symmetry). A very deep open question in physics is whether there is some more structured theory that explains exactly why these parameters have their values, or at least, how the parameters for different particles are related.
As a side node, the proton actually gets almost none of its mass from the Higgs field! That's because the Higgs mechanism only gives mass to fundamental particles in the theory, and protons are made up of quarks and gluons bound together in a potential of the strong nuclear force. The quarks within a proton are very light, and the gluons are completely massless, so it is actually the binding energy of these particles that yields the effective mass of the proton (this is E=mc^2 at work).
As someone who doesn't know what I am talking about, can I ask a stupid and naive question?
By converting energy into mass and mass into energy, would it be conceptually feasible to generate thrust in a closed circuit? My thinking is that you could use that for propulsion in space. We are currently relying on throwing stuff out to generate a reaction force and of course we quickly run out of things to throw. But if you could change the mass of particules in flight, you could increase the mass on the way forth and decrease the mass on the way back, generating continuous thrust?
Thanks. I must be missing something. If I have a particle emitted from point A and stopped in point B, travelling between the two at velocity v, and that I can magically change its mass in flight from M (when it leaves A) to m (when it reaches B), with M > m, wouldn't I create kinetic energy for the overall system of 0.5 * (M-m) * v^2 ?
In relativistic mechanics, the energy momentum relation holds: E^2 = p^2 + m^2, and energy is conserved in a closed system. If on a system with 1 particle the mass changes, the momentum must change to compensate as well.
In a closed system all three quantities would be preserved.
According to relativity, invariant mass is a property of a system of particles. You can not find it just by taking all the particles and adding their mass up.
A single photon has zero mass, but a system of two photons does have mass (except in the case where they are heading in the exact same direction) and if they do collide mass is preserved.
Mass is a type of energy. This means that inertia is dependent on energy not mass (I think). Converting some mass to energy would still require the same force to accelerate.
From a momentum point of view, photons behave as particles with their E=MC^2 mass and velocity C. If you bounce a laser off a mirror, it will exert a pressure which is equal to what you'd get from a (mass equivalent) stream of particles bouncing off it even though photons don't have mass.
> hoping to discover new secrets about the universe
I am curious as to what kind of new secrets. Because the recent examples - the discovery of gravitational waves and the Higgs only confirmed well-established theoretical predictions.
My guess: Those "new secrets" would be in the category of "unknown unknowns"[1]. We don't even know where to look for them, so we looked somewhere we hadn't before—in higher energies. And we used a "known unknown" as a stepping stone—the Higgs, which we were pretty sure existed, and we had an idea of what its properties would be.
Well said. Some particular examples of things we're looking for in this case, however, include supersymmetry, strong gravity / extra dimensions, and dark matter. All of these theories generally can be contrived one way or another to alter the predictions of the standard Higgs theory.
But we are also looking everywhere we can and trying to do precise measurements because we may find something surprising as well!
Do we have any experimental evidence of shortcomings of the standard model? It seems to me as a lay person that it keeps getting confirmed at higher and higher energies, and hints of science beyond it remain elusive. Is that true?
I have an unrelated question as you seem knowledgeable: Does the Quantum version of mass/gravity conflict with Einstein theory of general relativity/spacetime?
As a layperson, this is so confusing. On one hand, we have Higgs Bosons "giving" particles mass, presumably in a nondeterministic quantum manner, on the other hand we have relativity theory that says mass "warps" space-time itself. What is the relation between the two theories?!
Nobody knows. It's like knowing how electronics work, from transistors downwards; and how software works, from machine language upwards; but completely missing the entire concept of a CPU, how it's built, how complex (or not) it is, and how to study it and tinker with it. Quantum gravity is one of the biggest remaining mysteries or unknowns in Physics.
The short answer is that when doing quantum mechanics on curved spacetime, we tend to do it semiclassically: the quantum stuff is approximated or averaged, and then that is taken as the source of classical spacetime curvature. The averaged (or whatever) value of the Higgs field at a point in spacetime, like the value of all the other fields at the same point, is then just a contribution to the stress-energy tensor at that point in spacetime.
The Einstein Field Equations [1], dropping constants and indices, and with a vanishing cosmological constant, can be written as G = T. Here G is the Einstein tensor, which describes curvature at each point, and T is the stress-energy tensor, which describes the flux of momentum-energy through each point.
Below, for ease of understanding T, let's apply Cartesian-like coordinates (really, Minkowski coordinates, which are spatial Cartesian coordinates x,y,z and time coordinate t, such that when calculating distances between two Minkowski points the two sets of coordinates differ by a sign and a constant: ds = sqrt(dx^2 + dy^2 + dz^2 - c^2dt^2) is one way of writing out the line element in a Minkowskian fashion, but below let's use ds^2 = c^2dt^2 - dx^2 - dy^2 - dz^2, which is the "mostly-minus" or "+,-,-,-" metric signature; below we'll refer to this line element as "the metric". The metric is a component of the Einstein tensor G, and typically in the Einstein Field Equations you can see the metric exploded out as its own tensor g [2].
Let's look shallowly at the stress-energy tensor. We have made a deliberate choice of metric, and of coordinate basis, and will lean a bit on the natural spacetime slicing into space and time that these particular choices give us.
T can be written as a 4 x 4 matrix with rows and columns starting at 0 and running to 3. T_{00} or shorter T_00, two zeroes subscripting the letter T, means the 0th row and 0th column; 0 in our metric above means the time direction; 1 means the x direction; 2 means the y direction; 3 means the z direction.
With our set of choices, T_00 corresponds to \gamma m_0 c^2: it is the "matter" at a point in spacetime that has come from the past and is going to the future, and is not moving in the x, y, or z direction. "Matter" is all the contributions to energy-momentum. Here that's some expectation value for each of the quantum fields at the point.
T_ii means we look at T_00, T_11, T_22, T_33. Let's look at the he lower three of these diagonals, T_ii, i != 0, so we are not looking at T_00. With all these choices made, T_11 is the flux of x momentum in the x direction. If x is "left" and "right" then we are thinking about momentum going from left to right entering the point from the right and exiting the point to the right. Again, that momentum can be photons or any other quantum field content.
T_0i and T_i0 can be thought of momentum-energy which originates or terminates at the point, arriving or departing in the i direction; more precisely, if you know some special relativity, T_00 here looks like \gamma m_0 c^2 and T_0i looks like \gamma m_0 \vec{v}_{i} c.
For completeness, the non-diagonals, T_ij, i,j ! =0, i != j are the fluxes of i momentum the j direction, or equivalently with our choices, the total momentum times the velocity in the j direction.
So, considering the middle space of three 3d spaces at time coordinates t-1, t, and t+1, at a point p the stress-energy tensor T encodes the all the quantum field values and changes thereof that contribute to the energy-momentum that is constant at p (in T_00) or which arrive and depart p in the three spacelike directions. The momentum is deposited into the "matter" at the point and adjacent (but in the future light cone) points in spacetime we are looking at, and arrives from the matter the adjacent points in spacetime in the past light cone. [4]
When taking this sort of semiclassical approach we usually write G = <T> where the angle ...
To some, further confirmation of the standard model is a disappointment because it doesn't tell us anything we didn't already know or point to some exciting new physics.
Personally I'd prefer if the established physics we have stays put and the rest of new knowledge mostly falls into the (pretty big) gaps instead of shaking up the solid stuff. Because it seems like it's already complexified to a sufficiently high level.
Just trying to unpack your statement. Are you saying we're trapped because the standard model doesn't allow for FTL travel? (This is my assumption based on context)
I'm way outside my wheelhouse here for knowing what the standard model allows so please bear with me.
Yeah I thought about it for a bit and realized my question was pretty dumb if you understand that a basic underpinning of The Standard Model is that you can't exceed the speed of light.
Oh my, you're a big shot engineer and investor chap! Sorry, being British and something of a recluse, I don't really talk to people like yourself very often.
Now I wish I'd omitted the "but I could be wrong" so I'd have looked a bit more decisive — and, y'know, less guarded-because-I've-been-on-forums-long-enough-to-know-that-I-should-cover-my-ass-against-all-possible-scenarios.
Read this theory, it contains everything the standard model is incapable of explaining, i.e. mass, distribution of normal matter/antimatter dark matter and dark energy after the big bang, decrease of dark matter, increase of dark energy, what DM and DE actually is, et cetera:
No, the fundamental equation 1.1 and 1.2 is structurally similar to the Equation of Matter suggested in 1958 by Werner Heisenberg, except for two significant differences:
1) 1.1, 1.2 does not contain a dimensionful coupling constant
2) It contains the point-split which Heisenbergs equation is lacking of.
Do you understand any of this? This notation is entirely unfamiliar to me, and the text seems like gibberish (my favourite expression is "The most colossally great global unification"). I'm also a bit skeptical about one person answering so much big open questions all by himself, while there are a lot of very bright scientists working on them without this much success.
I do, we are talking about a non-linear spinor dynamic here, omitting the gamma algebra inherited by Dirac spinors. This algebra is well known and omitted as it would render the text confusing indeed as spinor products are of relatively high order (psi-27 and psi-19).
No references. The fundamental idea is based on the Equation of Matter suggested in 1958 by Werner Heisenberg. Anything else is new. This theory solves the problems, Heisenberg introduced with his equation by eleminating the coupling constant l (dim psi = -1/2 hence not observable instead of -3/2) and adding the point split on the right side of the equation which is a consequence of the differential operator on the left side (dx is equivalent to the point split). The rest naturally follows from this fundamental equation.
From skimming the pdf, I didn't notice any conventional equations such as one would find in a paper by someone like Heisenberg. If there were any, could you point one out?
Edit/post script:
I also don't see that the word "algebra" is mentioned in the document at all. By comparison the Wikipedia page on spinors uses the word "algebra" 116 times. That seems odd if this theory is based on a deep understanding of spinors.
The word "colossal" appears a surprisingly large number of times, as I just posted elsewhere in this thread. And "rupture" is used even more. You would think such important words would have some introduction, unless they are standard terms of art.
Well “rupture” in this context simply describes the rupture of the massive short ranged repulsive boson G5 leading to the rupture of the neutrino leading to the reproduction cascade (see p153) leading to the proportions of normal matter/antimatter and dark matter as measured by the planck telescope right after the big bang.
Can you define "rupture" without using the word "rupture" or "simply" in the explanation?
I find the excessive use of "colossal" and "rupture" to be very suggestive of a Freudian slip implying the author is subconsciously aware that his inspiration followed a massive cerebral hemorrhage.
This reminds me of the thick manila envelopes I got in the mail at university. "I have discovered a proof of Fermat's Last Theorem that is at most two pages long." Starts off with the wrong definition of a prime number. Ugh!
Your link reminds me of those manila envelopes. Cargo cult science indeed!
I seriously do not understand why this question would be downvoted?
It's almost as if your question is being interpreted as either:
1) as defense of the manila envelope (how is a question a defense?)
2) as indicating you are the author of the envelope (that probability would be incredibly low!)
3) as being written by the same author who made some other unliked comment in this topic (since when do we downvote all comments of an author as soon as we dislike one of his comments?)
The downvote means: "I cannot tell whats wrong with the theory b/c I didnt even read it. I don't know what a spinor is, nor am I familiar with the concept of point splitting. I dont even understand why the coupling constant is superfluous b/c I always thought the dimension of a spinor is -3/2 instead of -1/2."
But downvoting in the first place seems reasonable.
Not trying to attack the standard model here but rather showing interest in discussing a new approach.
I can't comment on advanced math, but there are a number of things that I do not associate with real scientific papers:
1. Not prepared with LaTeX.
2. Photo of the author.
3. Obsession with rounded rectangles and ovals.
4. It uses the word "colossal" 83 times and "rupture" 110 times.
5. Didn't see any references to other scientific works.
This is fantastic!
Standard level as crackpottery goes but visuals are great, he took it to the whole new level, beats all the other html or LaTeX ones. That pdf took a while to format.
The visuals are great indeed. Same is your reading speed. Now improve your level of understanding text as well while being distracted from beautiful visuals.
Yeah, they are spectacular. And then you look at the green parts on the side and realize that thing is 4 stories high.
As an aside, I like the understated way the description is written:
The extraction of these events from the LHC data is challenging as there are many mundane type of events that can mimic them. Identifying these events requires measurements from all CMS subdetectors, which makes the reconstruction quite complex.
I can only imagine what the value of "many" and the amount of effort behind "challenging"and "quite complex" really is.
What I find incredible is the drive that these scientists have; then again they get to work at what is in my opinion the most amazing scientific facility humanity has built to date on Earth.
I'd choose looking over mundane data every day for that, regardless of how boring it was, if only to be in the shadow of giants.
A friend of mine, during his PHD defence on some theoretical physics topic that is way beyond me, once used the term "garden variety quantum(something)", to distinguish it from the new crazy theoretical dimensional weirdness he had been researching.
(actually the phrasing was quite a bit funnier in Dutch: "huis- tuin- en keukenquantum")
I was a bit involved in the ATLAS result. IMHO, it's not really that fancy. Basically, there's a boosted decision tree that is used to select signal-like events, and it was re-optimized some new features and a larger training set. Also, they dropped a statistical categorization that was of interest for a related process in favor maximizing sensitivity to this ttH production mechanism specifically.
I haven't looked too carefully at the CMS result, so no comment there.
CMS physicist here! As our ATLAS colleagues, we also use boosted decision trees extensively in our analysis, as well as the so-called Matrix Element Method -- a way to combine the knowledge of the differential theoretical cross-sections for the signal and background processes with our knowledge of the experimental resolution of our detectors. More details are available in [1].
However, in CMS we have recently started using Deep Neural Networks. These are used for the separation of signal and background events in the "single-lepton channel" of the search, i.e., the search where the Higgs boson decays to two bottom quarks and the top quarks decay in such a way that at least one electron or muon is present in the final state. Again, more details here: [2]
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[ 2.0 ms ] story [ 204 ms ] threadThe next question from that was - is that really the Higgs Boson, does it behave the way we expect it to (according to standard model)? I believe this is a test to verify that it does and they measured the coupling constant and it matched up. Neat. This could help with a much deeper understanding of why particles have mass.
Interestingly, the primary production mechanism for the Higgs boson at the LHC proceeds via the fusion of gluon particles from the colliding protons. This seems strange at first glance, since the Higgs interacts with particles proportionally to their mass, while the gluons are massless. In the standard model, there is a higher-order process wherein the gluons annihilate into a virtual "loop" of top quarks (which are very massive), which then "lend" their mass to produce the Higgs.
Because previous measurements have been consistent with the Standard Model prediction, we already had some evidence that the coupling to top quarks was nominal. However, there are other possible scenarios involving exotic physics that could mimic this production mechanism, which could imply the existence of new forces/particles, and that the Higgs boson does not couple to "normal" particles in the predicted fashion. Because of the nature of these heavy virtual loop processes, it turns out that it's pretty hard to distinguish between different such scenarios by examining the kinematic properties of the events. Hence, the main observable is the rate, and even that can be made to match a wide range of values with or without standard couplings, given a clever enough theory.
This recent result demonstrates directly that the Higgs boson does indeed couple to the top quark in a matter roughly consistent with the Standard Model expectation (the CMS measurement shows an upward fluctuation, indicating even stronger coupling than expected, although this is probably just a statistical fluctuation). Therefore, no fancy/exotic physics (such as string theory, strong gravity, etc) are required to explain the observed production of Higgs bosons so far at the LHC.
There is a certain beauty in not only accepting that you might be wrong, but actively wanting to be wrong because that could be so much more interesting!
And a certain sadness in the disappointment some obviously have when they accept that the less interesting outcome is the one that they receive.
"I'll call it 'Aluminum.' No, wait! 'Aluminium!' Uh... ship that first print run of my book with the wrong spelling to North America. Nobody will notice!"
"I'll call it Potassium, because it's found in potash." "That's not very creative." "Fine, I'll call it Kalium and give it a symbol of K." "Where'd you get Kalium from?" "Well, it's very alkaline, you see. It's from potash, after all." "That's still not very creative!" "Fine. We'll call it Potassium, but give it a symbol of K. Happy now?"
And those are also mostly the countries using Kalium: https://en.m.wiktionary.org/wiki/kalium
https://en.wiktionary.org/wiki/%E3%82%AB%E3%83%AA%E3%82%A6%E...
This is possibly the most highly-cited statistics paper in our field: https://arxiv.org/abs/1007.1727 It provides asymptotic formulae that allow us to estimate these p-values without having to simulate our experiment tens of thousands of times. But it also gives a nice overview of the different test statistics one might use.
"LHC Statistics for Pedestrians" is short and informative, but a bit haphazard and probably assumes you're familiar with a lot of jargon: https://cds.cern.ch/record/1099994/files/p205.pdf
"Practical Statistics for the LHC" is a much more complete and thorough introduction, but it's quite long and technical: https://arxiv.org/abs/1503.07622
"Statistics for searches at the LHC": https://arxiv.org/abs/1307.2487 Similar to the previous one, but maybe more words and less math. Perhaps one of these will resonate with you more than the others!
Lastly, here is a public note that was created jointly by the ATLAS and CMS collaborations prior to the Higgs boson discovery. Basically, we got together and came up with a consistent way to present new results from the LHC, and this note documents those protocols: https://cds.cern.ch/record/1379837
I don't see the purpose of question number 1, it seems totally spurious. All you need to care about is how well the various models explain the data.
EDIT:
For example, with the famous "sun's gravity bending starlight" example they compared the observations with predictions due to Newtonian gravity x with predictions due to Relativity 2x, there was no need to check for zero deflection since there was no theory predicting that. However, if some value (including zero) inconsistent with both was observed a new theory would need to be developed. Then that theory would need to be tested on some other phenomenon.
You don't just try to find the model that best fits the data and claim a discovery if this isn't your null hypothesis. Rather, the data needs to be far enough away from that predicted by your null hypothesis that it is highly improbable that you would find data at least that far from the prediction if the null were true.
For instance, in your example, if they had observed 1.8x, but the uncertainty on that were 0.8x, no discovery would be claimed despite the relativistic model explaining the data better than the non-relativistic model.
The data is consistent with the predictions of both models in this case. If we want to distinguish between them we need to get more/cleaner data or different data to compare to different predictions. What is wrong with that?
>"You don't just try to find the model that best fits the data and claim a discovery if this isn't your null hypothesis."
This is not what I am suggesting to do, see above.
>"Rather, the data needs to be far enough away from that predicted by your null hypothesis that it is highly improbable that you would find data at least that far from the prediction if the null were true."
What purpose does this serve?
EDIT:
Here is a venn diagram of what I mean, with four possibilities: https://image.ibb.co/c432OT/venn_Science.png
You are saying for some reason it is important check for !B which equals regions A - (A or B) + !(A or B). Why?
Why not just check which corresponds to the results? Is it model A only, model B only, model A and model B, or neither model A nor model B?
In principle that's fair enough, but in practice, the Standard Model has already passed lots of tests -- it fits the results of many, many experiments -- so we already have a high confidence that it's correct (or rather, a very close approximation to the truth for all the experiments we're been able to try). So brand new model B does not start on an equal footing. The null hypothesis is "model A is correct".
If there's some new experimental result that does not fit with the Standard Model -- and this usually not a clear-cut thing, but a statistical estimate of likelihood -- but does fit model B, that's a useful new result. If the error bars are such that it fits both models, you stick with the tried and tested model A, unless B has some compelling new advantage (like being much simpler than the Standard Model, say) and it also fits all other existing experimental data.
Also model A may be something like "Standard Model w/o sterile neutrinos", while model B is "Standard model w/ sterile neutrinos". My understanding is these will be supported by all the same previous evidence.
And anyway, if you want to include prior info there is a principled method of doing so: Bayes' Rule. The method described here is indirect, obfuscated, qualitative, and open to all sorts of bias. In general it seems inferior in every which way, why has Bayes' Rule been rejected for this purpose?
In that specific case, no, a number of existing experiments appeared to confirm the "w/o sterile neutrinos" model, so it was assumed that was correct. Just one older experiment fit the "w/ sterile neutrinos" model; that has only recently been reproduced successfully, so now that model is back on the table. But it's still possible that it's just a measurement error.
And anyway, if you want to include prior info there is a principled method of doing so: Bayes' Rule. The method described here is indirect, obfuscated, qualitative, and open to all sorts of bias. In general it seems inferior in every which way, why has Bayes' Rule been rejected for this purpose?
Good question, I don't know! I wonder if some of the LHC people commenting here can talk about the reason for sticking with Frequentist over Bayesian statistics?
I suspect this gets into some pretty deep issues around the philosophy of science. Are we looking for the "correct" theory, or just successively better approximations to reality, or what? I don't think you can easily say "the Standard Model is incorrect" -- we know it's incomplete, hence incorrect, but it also fits experimental data incredibly well, so it must be a close approximation to some level of reality at the very least.
(edit to clarify: what I mean is, I'm not sure how you set a prior confidence on "is the Standard Model correct?" in a Bayesian sense, since we already know it's partially correct and partially incorrect.)
I was talking about all the other types of observations used to support the standard model. Afaik the existence of sterile neutrinos would not change the predictions.
>"Good question, I don't know! I wonder if some of the LHC people commenting here can talk about the reason for sticking with Frequentist over Bayesian statistics?"
It isn't really a matter of frequentist vs bayesian statistics. Frequentist stats looks like what you see in Figure 1 here (my venn diagram is just a simpler version of it): http://rsta.royalsocietypublishing.org/content/231/694-706/2...
However, it is put forward that prior information should be involved in interpreting the results of the significance test. This idea has been rejected by all the giants and founders of modern stats (Fisher, Neyman, Pearson, etc). Its just some ad hoc thing come up with by stats 101 authors.
>"I suspect this gets into some pretty deep issues around the philosophy of science. Are we looking for the "correct" theory, or just successively better approximations to reality, or what?"
We're supposed to be comparing the predictions derived from our theories/models to data collected after the prediction was made and use these predictions to come up with useful tech and perform amazing feats.
>"I'm not sure how you set a prior confidence on "is the Standard Model correct?" in a Bayesian sense, since we already know it's partially correct and partially incorrect.)"
The current solution seems to be performing an elaborate ritual that obscures the true method of using collective opinion.
For instance, the Higgs is part of the Standard Model but for the Higgs discovery the null hypothesis was that the Higgs does not exist.
Yes, I know. This isn't at all a positive thing as you seem to think...
I've been lately seeing that this practice is infecting particle physics, which is not a good sign. I do not think they are overwhelmed yet though. Here is how it has gone in every field so far (education research, psychology, medicine, etc):
Eventually the field will stop caring about all actual quantitative predictions (some barely funded crackpots on the edges will publish in ignored journals) and researchers will only test a "null hypothesis" that everyone knows is wrong (eg, in the physics case a world where the standard model is assumed true but has no higgs boson). Then upon rejecting the (known to be false) null hypothesis, they will conclude some theory only capable of vague/malleable predictions is correct.
The way it works is simple, the null model acts as a strawman. The confidence in rejecting the null model is somehow translated into support for the researcher's favorite theory. How does changing the significance level address this problem?
Not just any old favorite theory. For instance, an excess at a mass of 125 GeV doesn't provide any evidence for a new particle at 2 TeV. It does however provide evidence for a new particle at 125 GeV.
> Eventually the field will stop caring about all actual quantitative predictions (some barely funded crackpots on the edges will publish in ignored journals) and researchers will only test a "null hypothesis" that everyone knows is wrong (eg, in the physics case a world where the standard model is assumed true but has no higgs boson). Then upon rejecting the (known to be false) null hypothesis, they will conclude some theory only capable of vague/malleable predictions is correct.
If that were the case, we would have made a lot more discoveries by now.
In physics you still have quantitative predictions done in addition to checking the null hypothesis (which I why I said that was superfluous), if NHST adoption continues these will slowly be deprecated and replaced by only checking the null hypothesis. Seriously go read some old psychology before NHST destroyed it, they were developing quantitative theories of learning and everything [1,2]. Then go look at it now (statistically significant this and that with basically no progress for 60 years...).
Also, the significance level, constraints on p-hacking, etc are adjusted so that discoveries occur at the "right" rate. I'm not sure what triggered he move to 5 sigma in physics but it was probably something like "this seems too easy" so people started carefully double checking and getting conflicting results.
[1] https://www.tandfonline.com/doi/pdf/10.1080/00221309.1934.99...
[2] https://link.springer.com/article/10.1007/BF02289265
Nevertheless, I suppose what you would suggest is just setting limits to start with and looking for a bump there instead. That's not a bad idea, and some (Gross, e.g.) have suggested setting limits even in discovery papers.
I don't see how this addresses any of the issues, it just makes it more expensive (ceteris paribus). As I already wrote:
"A more stringent significance level just means it costs more money or the data is much cheaper to collect. ...The way it works is simple, the null model acts as a strawman. The confidence in rejecting the null model is somehow translated into support for the researcher's favorite theory. How does changing the significance level address this problem?"
>"Nevertheless, I suppose what you would suggest is just setting limits to start with and looking for a bump there instead."
Exactly, and the more precise the limits, the more meaningful for the theory if its consistent with the data. At the extreme, theories that allow for any value at all (as I understand the case is for every possible observation under string theory) are not supported by the data no matter how it turns out.
Confidence in rejecting the null isn't "somehow translated into support for the researchers' favorite theory", it's translated into support for the existence of a signal, which makes sense since the null is the background-only hypothesis.
After we establish rudimentary support for a model by finding one or more such signals, we can then embark on the process of doing precision measurement to really test that model (as is being done for the SM).
If its only a statistical fluctuation, the p-value due to sequential sampling follows a markov process (random walk) between zero and one (there is no convergence). So starting from a significant result, the p-value would be just as likely to decrease and become "more significant" as increase and "lose significance". The significance cutoff is irrelevant to this behavior, although the random walk will spend less time in these extreme regions to begin with.
Here is an example of the random walk in R. It was my first attempt when going up to 100k samples, after n = 45 the p-value was ~5e-4 (~3.3 sigma), later at n = 36441 it went even more extreme in the other direction, corresponding to a p-value of ~1.9e-6 (~4.65 sigma). Here is the plot and code: https://image.ibb.co/hOHO08/p_markov_chain.png
Perhaps I'm wrong and if you run enough of these and subset to only look after a certain threshold has been breached (ie 5e-2 or 3e-7) there will be different behavior, I doubt it though. However, that is all unimportant since it is based on a false premise:>"_if_ what you're seeing is a statistical fluctuating"
You aren't you are seeing that, so everything that follows is irrelevant. The background model is imperfect (eg nobody believes in a standard model with no higgs boson, everyone knows it is wrong somehow). In this (realistic) case convergence to statistical significance is guaranteed with enough data. However, in the rare (non-existent?) case where the background model is thought to be perfect, it is a different story.
>"Confidence in rejecting the null isn't "somehow translated into support for the researchers' favorite theory", it's translated into support for the existence of a signal, which makes sense since the null is the background-only hypothesis."
This amounts to claiming that in most peoples minds (including the authors of the paper) the Higgs boson, gravitational waves, etc haven't been "detected with 5 sigma confidence"... How much would you want to bet on this? The null model could be rejected due to a loose cable (ftl neutrinos), but the p-value doesn't distinguish between these explanations. Perhaps there was "a loose cable" in the LHC experiments but nobody looked very hard since the deviation agreed with preconceived notions? The p-value doesn't help you here.
>"After we establish rudimentary support for a model by finding one or more such signals, we can then embark on the process of doing precision measurement to really test that model (as is being done for the SM)."
Why not just skip the first step? Instead collect data to check whatever models that exist. When none of them can explain it, modify or come up with new models until it fits. Then derive new predictions from those and collect new data to check them, repeat.
EDIT: I ran it again and got this: https://image.ibb.co/g9rGL8/p_markov_chain2.png
If you collect, say, 1000 samples of a normally distributed variable and find that the mean (for instance) is 2 sigma from the expected mean, then if you collect another 1000 samples and take the mean of all 2000 samples, you will probably find that the significance decreases, assuming the first result was a statistical fluctuation. This is just [regression to the mean](https://en.wikipedia.org/wiki/Regression_toward_the_mean).
What we don't do is dishonestly drip-feed data until we hit the significance we want, then stop. Data is added in fairly large chunks (generally an year's run at a time), and when a new dataset is added the analysis is developed with (at least the new) data blinded. The dataset is only unblinded when the analysis has been finalized.
You have found a deviation from your null model. That is it.
>"so it's right to claim a discovery."
No, if you knew the null model was flawed to begin with nothing has been learned. Also I wouldn't refer to something like "equipment was malfunctioning" as a discovery. Drawing any conclusions about the actual research hypothesis must be done outside the NHST framework, or else there is a fallacy at play (probably strawman).
>"What we don't do is dishonestly drip-feed data until we hit the significance we want, then stop. Data is added in fairly large chunks (generally an year's run at a time), and when a new dataset is added the analysis is developed with (at least the new) data blinded. The dataset is only unblinded when the analysis has been finalized."
Great, but even if you don't p-hack it still doesn't work unless it really makes sense to assume the null/background model is perfectly true. P-hacking is just more BS on top of an already BS procedure.
In summary: If there is anything wrong with the null/background model at all, the p-value will converge on zero, it is just a matter of collecting enough data. This will happen regardless of whether the theory of interest (research hypothesis) is accurate or not.
We don't know that the null is flawed to begin with. Not in a way that matters to the analysis anyway, otherwise you've picked the wrong null. No one runs analyses to discover the pion for the millionth time.
For BSM work, the way it generally works is this (ignoring limit setting):
- Pick a signature predicted by one or more BSM models (or even none), that either isn't predicted by the SM or is exceedingly rare in the SM. For example, you might predict a new particle that decays in some predetermined way.
- Define a signal region in some combination of variables where you expect to find a signal corresponding to this signature. This region is blinded, and you don't look at it until after fixing your entire procedure.
- Estimate the background in this signal region with a combination of Monte Carlo simulations and extrapolation from outside this region (data-driven backgrounds). This obviously has both statistical and systematic uncertainties, and a lot of the hard work is in getting this right. For instance, you might use independent Monte Carlo generators, or define control regions to check your estimation in.
- "Open the box" and look at the signal region data. If you see an excess over the estimated background, calculate the significance. Even here, if you were looking for a new particle, for instance, and the excess isn't a localized bump, this would be an indication that the background estimation may be flawed.
- If the significance is over 5 sigma, you have a discovery.
As you can see, you aren't using a null hypothesis that you already know is flawed. Your null is specifically "no signal exists". A positive deviation that isn't a statistical fluctuation is by definition a discovery of a signal.
Things like malfunctioning equipment go into the uncertainties if they occur in a way that the researchers have considered (which often means uncertainties are set conservatively if the equipment behaviour is poorly understood). If they occur in a way that no one considered, there's no statistical trickery that's every going to compensate for that. If we just went straight to setting limits, we would still see a deviation from what's expected there if equipment malfunctioned in a manner that faked a signal.
> In summary: If there is anything wrong with the null/background model at all, the p-value will converge on zero, it is just a matter of collecting enough data.
In summary: Assuming the background estimation is correct, the p-value will only converge to zero if a true signal exists. If the background estimation is wrong, then the background estimation is wrong and this is a problem with the background estimation, not hypothesis testing.
I'm by no means claiming the system is perfect, but it isn't systematically flawed the way you seem to be claiming.
>"Assuming the background estimation is correct, the p-value will only converge to zero if a true signal exists."
Aren't you assuming the background model is correct and a true signal exists?
>"Your null is specifically "no signal exists"."
No, it is never this. It is an entire model, one assumption of which is "no signal exists". The p-value doesn't care which assumption is wrong, it is only wishful thinking that leads to people focusing on that one.
>"We don't know that the null is flawed to begin with."
Sorry, I don't believe this. Give a concrete example. Do you believe the standard model is 100% correct? If not, then any background derived from it must be assumed to be flawed to begin with.
>"Things like malfunctioning equipment go into the uncertainties if they occur in a way that the researchers have considered (which often means uncertainties are set conservatively if the equipment behaviour is poorly understood). If they occur in a way that no one considered, there's no statistical trickery that's every going to compensate for that."
Correct, there is no statistical trickery to compensate for this. It is a scientific problem, not statistical.
Did you check out that Meehl paper I linked elsewhere?[1] If you take a prediction of a model and test that, messing up the experiment means you get results that diverge from your prediction. If you reverse the logic of science so that you test the "opposite" of your prediction, messing up the experiment yields results that seem to support your model. This is why the prediction of the theory needs to be set as the "hypothesis to be nullified".
[1] https://meehl.dl.umn.edu/sites/g/files/pua1696/f/074theoryte...
1. If you're using a data driven background, you're background model isn't the Standard Model but that there isn't something special about your signal region.
2. If you are using the SM as your background, then yes you do believe it to be 100% true, since what you are looking for is evidence that there exists new physics not described by the SM.
In other words, the theory under test is the SM, and it can pass very easily. If it fails despite this, that's evidence that it's incomplete. If it passes, the limit setting stage tests whatever new physics we were looking for, and gives an upper bound on how sure we are that it does not exist.
Sure, it means you assume that during the signal detection everything was working exactly as it was during background data collection. There are going to be other implementation specific assumptions like what thresholds to use regarding environment noise triggers, accounting for sensor drift, etc. These data-driven models are approximations, I doubt the people actually coming up with them really believe they are 100% true. If you give a real life example I will point out exactly where there are issues.
> "If you are using the SM as your background, then yes you do believe it to be 100% true"
I don't know what this is supposed to mean. Of course you are assuming your background is 100% true. Do particle physicists actually believe this though? Not from my reading:
"So although the Standard Model accurately describes the phenomena within its domain, it is still incomplete." https://home.cern/about/physics/standard-model
As for the SM, we are looking for those places where it is incomplete, and to do this we must assume it is complete and look for strong evidence that we are wrong. To date, it doesn't seem like we see though, as far as collider physics is concerned.
I know you're feeling very right and vindictive but damn if this isn't tiring to read. Make sure you know what you're right about first before assuming the other thing is wrong just because it matches a few keywords that you've read are bad. Because assuming good faith means that you allow for the possibility they might not be doing it wrong. You still get to make your point but it saves your face a lot.
I'd suggest, go outside, attack a windmill for a few hours, think about what you're actually trying to say, and if it's not "hey I read this article on lesswrong and it says everybody is doin it wrong", you'll probably find you can make your point much clearer.
You seem to have more than sufficient knowledge about statistics to think for yourself on this matter.
Quote this. Where? I am sure by "corrected" you mean "someone claimed something I believe to be wrong, so I continued to point out why." Amazingly, this looks like yet more strawman arguing...
For one more point, we pick the null hypothesis so that we can when we collect data we can calculate probabilities of that data assuming the null hypothesis is true. So, what null hypotheses we can consider are both enabled and constrained by the assumptions to calculate the probabilities given the data.
That is an awful reason to choose a null hypothesis. You should choose a null hypothesis you derived from your theory so you can see if your theory is capable of making accurate predictions.
Your alternative hypothesis is derived from your theory.
>"In the physical sciences, the usual result of an improvement in experimental design, instrumentation, or numerical mass of data, is to increase the difficulty of the “observational hurdle” which the physical theory of interest must successfully surmount; whereas, in psychology and some of the allied behavior sciences, the usual effect of such improvement in experimental precision is to provide an easier hurdle for the theory to surmount."
https://meehl.dl.umn.edu/sites/g/files/pua1696/f/074theoryte...
> I'd suggest starting with Meehl 1967
Your very quote states that this whole idea works for physics, and is describing that it doesn't work in psychology and social sciences. I'm confused by this:
To take the IQ example, if you take the set of all people in a country, for instance, and randomly select two sets of 5 people, you will find that their average IQ differs by some amount. If you instead select two sets of 50000 people, the average IQs should be a lot closer (to each other, and to the true average). This is by definition true, since IQ is by definition normally distributed. If that's not what you see, you have a methodological problem.
>"Because physical theories typically predict numerical values, an improvement in ex-perimental precision reduces the tolerance range and hence increases corroborability."
I don't know the historical details but it would appear that since 1967 the NHST virus has proceeded to begin its infestation of physics. Now physicists are acting more and more like psychologists (focusing on testing a null model rather than the predictions of their models; which is the first phase of the illness) and will reap the same consequences of stagnation, etc. Lowering the threshold to 3e-7 instead of 5e-2 just makes this slower and more expensive.
>"To take the IQ example, if you take the set of all people in a country, for instance, and randomly select two sets of 5 people, you will find that their average IQ differs by some amount. If you instead select two sets of 50000 people, the average IQs should be a lot closer (to each other, and to the true average). This is by definition true, since IQ is by definition normally distributed. If that's not what you see, you have a methodological problem."
I'm not sure why you are talking about standard errors of random samples from a population... He was just giving stats 101 background for philosophers so he could get to this point:
"While no competent psychologist is unaware of this obvious distinction between a substantive psychological theory T and a statistical hypothesis H implied by it, in practice there is a tendency to conflate the substan- tive theory with the statistical hypothesis, thereby illicitly conferring upon T some-what the same degree of support given H by a successful refutation of the null hypothesis. Hence the investigator, upon finding an observed difference which has an extremely small probability of occurring on the null hypothesis, gleefully records the tiny probability number “p < .001,” and there is a tendency to feel that the extreme smallness of this probability of a Type I error is somehow transferable to a small probability of “making a theoretical mistake.”
In addition, there's a difference between saying "p is low so it is unlikely that the null is true" which is absolutely correct, and "1 - p is the probability the alternative hypothesis is correct". Certainly in physics people don't believe the second, I don't know about social sciences.
The role of the test in a scientific theory was deeper than my statement!
In the main, novel hypothesis test I invented and published, there was more than just what I outlined and you criticized, more along the lines you mentioned: That "more" was something like "if the next observation is a long way from anything we've seen before, then maybe it is an anomaly?". The actual work of the math in the paper showed, intuitively, what "a long way" meant and, in particular, for the math, how actually to calculate, along the lines of my statement, the hypothesis test false alarm rate. So, in short, in nearest neighbors anomaly detection, with meager assumptions, we actually can calculate false alarm rate and, thus, get an hypothesis test.
And, then, we are not limited strictly to the single nearest but can do some weighted sum over several of the relatively near. Right, such things appear to be necessarily close to multi-variate probability density estimation. But such estimation commonly requires so much data that it is not a good, direct way to calculate or estimate probabilities; curiously we can do well with the calculations without actually getting a local density estimate although in a sense we are close to doing that.
The other remarks here are even better, e.g., get to how to do science, maybe at the LHC or some such. Good and beyond what I tried to say.
i always wondered how does standard model includes/describes these?
As far as I know, there's nothing too exotic (from a theoretical perspective), about tetra/pentaquarks. They are just QCD bound states of more than 3 quarks. The problem with QCD is that it's a non-perturbative theory, so we generally can't even do a good job computing the hadronic bound states that we already know exist!
So, I get the impression that these observations are mostly of interest to people doing QCD on the lattice (or other calculational methods), as inputs to their modeling. I.e. perhaps having an "answer key" for some tetraquark masses will allow them to better determine whether they should be modeling these states as bound states of two mesons (which each have 2 quarks), or as a totally different 4-quark structure.
Why are the words "loop" and "lend" in quotation marks? Are they just a handy visual a lay person would understand to describe a more complicated phenomenon? Is there no better word to describe what is happening, including within your field, but it isn't a technically accurate description?
I'm envisioning a room full of highly educated folk excitedly talking over each other... "Well it looks like a ring, but it doesn't quite meet up..." "It looks like a disc, but with more 'weight' to it..." "No, it looks like a loop-the-loop on a roller coaster!"
https://en.wikipedia.org/wiki/One-loop_Feynman_diagram
In quantum field theory, perturbative physical processes can be expressed as the sum of all possible diagrams compatible with the initial and final state of interest. Each diagram corresponds to an integral, and diagrams that have loops are special because they are underconstrained by the initial/final conditions. Hence, you are left with an additional integral over every possible combination of momenta that can be exchanged within the loop. These integrals are usually hard or impossible to compute and may require weird mathematical techniques (like dimensional regularization). So, yes, (theoretical) particle physicists talk about loops a lot!
"Lend" here is total b.s. that I made up. The point is that the gluons can't directly interact with the Higgs boson, so they use their collisional energy to create some massive top quarks that can.
In all seriousness, I'm just interested in how much is being obscured when folk like Cox do a TV show, obviously written for those interested but not involved like myself. I've no idea what anything in your paragraph meant past the word "In" (yes, the first word), but I can definitely picture a loop, and get that there is a something which is transmitted / moves / traded / otherwise-not-at-its-origin within that loop, and trying to understand what that something is will leave me drooling into the carpet.
Still, I'm glad I asked. Thanks!
"Virtual particles" implies they're somehow not real, but I assume the theory says they do have a real physical existence in some sense -- they have an influence on the real particles. Are they "virtual" just because they're extremely hard to isolate, so all our practical experiments are indirect, or are they different in principle from the normal, "real" particles that our experiments work with? Is it a qualitative or just a quantitative difference?
Would it be roughly correct to say that virtual particles by definition always vanish (mutually annihilate, etc, whatever) before the measured outcome of an experiment, therefore they definitely cannot be directly observed? But they're an integral part of the model, therefore if the model is correct, they really do have a real physical existence (in some complex quantum sense)?
Here's their 7-part series on Quantum Field Theory: https://www.youtube.com/playlist?list=PLsPUh22kYmNBpDZPejCHG...
An excerpt from part 5, "The Secrets of Feynman Diagrams":
The overall interaction described by a set of Feynman diagrams is defined by the particles going in and the particles going out. These are the particles that we actually measure. We know their properties - for example, their energy and momentum. And they obey Einstein's mass-energy equation. We say that these particles are on the mass shell, or just on shell. They sit on the shell structure you get when you plot Einstein's equation of energy, momentum, and mass. On the other hand, everything that happens between the ingoing and outgoing tracks has questionable reality.
Each possible diagram that results in the same ingoing and outgoing particles is a valid part of the possibility space for that interaction. The particles that have their entire existence between vertices within the diagram but don't enter or leave are called virtual particles. Their correspondence to anything resembling real particles is debatable. They are also, by definition, unmeasurable. Otherwise, they'd be one of our ingoing or going particles. These particles do not obey mass-energy equivalence. So they are off shell. These particles aren't even limited by the speed of light or the direction of time, which leads to all sorts of fun.
And thanks for the link.
A proton or neutron has a mass of approximately 1 GeV/c^2.
The Higgs boson has a mass of about 125 GeV/c^2 -- so it's totally appropriate to think about it as being 125x heavier than a proton, or about as heavy as an Iodine nucleus.
The top quark has a mass of 170 GeV/c^2 -- it's the most massive fundamental particle we've discovered so far!
Depending on the particle: https://www.youtube.com/watch?v=Ztc6QPNUqls
As a side node, the proton actually gets almost none of its mass from the Higgs field! That's because the Higgs mechanism only gives mass to fundamental particles in the theory, and protons are made up of quarks and gluons bound together in a potential of the strong nuclear force. The quarks within a proton are very light, and the gluons are completely massless, so it is actually the binding energy of these particles that yields the effective mass of the proton (this is E=mc^2 at work).
I could be wrong as I’m a layman in these things.
Yes, you are ;)
Start here: https://home.cern/about/physics/z-boson
By converting energy into mass and mass into energy, would it be conceptually feasible to generate thrust in a closed circuit? My thinking is that you could use that for propulsion in space. We are currently relying on throwing stuff out to generate a reaction force and of course we quickly run out of things to throw. But if you could change the mass of particules in flight, you could increase the mass on the way forth and decrease the mass on the way back, generating continuous thrust?
In relativistic mechanics, the energy momentum relation holds: E^2 = p^2 + m^2, and energy is conserved in a closed system. If on a system with 1 particle the mass changes, the momentum must change to compensate as well.
According to relativity, invariant mass is a property of a system of particles. You can not find it just by taking all the particles and adding their mass up.
A single photon has zero mass, but a system of two photons does have mass (except in the case where they are heading in the exact same direction) and if they do collide mass is preserved.
I am curious as to what kind of new secrets. Because the recent examples - the discovery of gravitational waves and the Higgs only confirmed well-established theoretical predictions.
[1] https://en.wikipedia.org/wiki/There_are_known_knowns
But we are also looking everywhere we can and trying to do precise measurements because we may find something surprising as well!
(IANAP)
The Einstein Field Equations [1], dropping constants and indices, and with a vanishing cosmological constant, can be written as G = T. Here G is the Einstein tensor, which describes curvature at each point, and T is the stress-energy tensor, which describes the flux of momentum-energy through each point.
Below, for ease of understanding T, let's apply Cartesian-like coordinates (really, Minkowski coordinates, which are spatial Cartesian coordinates x,y,z and time coordinate t, such that when calculating distances between two Minkowski points the two sets of coordinates differ by a sign and a constant: ds = sqrt(dx^2 + dy^2 + dz^2 - c^2dt^2) is one way of writing out the line element in a Minkowskian fashion, but below let's use ds^2 = c^2dt^2 - dx^2 - dy^2 - dz^2, which is the "mostly-minus" or "+,-,-,-" metric signature; below we'll refer to this line element as "the metric". The metric is a component of the Einstein tensor G, and typically in the Einstein Field Equations you can see the metric exploded out as its own tensor g [2].
Let's look shallowly at the stress-energy tensor. We have made a deliberate choice of metric, and of coordinate basis, and will lean a bit on the natural spacetime slicing into space and time that these particular choices give us.
T can be written as a 4 x 4 matrix with rows and columns starting at 0 and running to 3. T_{00} or shorter T_00, two zeroes subscripting the letter T, means the 0th row and 0th column; 0 in our metric above means the time direction; 1 means the x direction; 2 means the y direction; 3 means the z direction.
With our set of choices, T_00 corresponds to \gamma m_0 c^2: it is the "matter" at a point in spacetime that has come from the past and is going to the future, and is not moving in the x, y, or z direction. "Matter" is all the contributions to energy-momentum. Here that's some expectation value for each of the quantum fields at the point.
T_ii means we look at T_00, T_11, T_22, T_33. Let's look at the he lower three of these diagonals, T_ii, i != 0, so we are not looking at T_00. With all these choices made, T_11 is the flux of x momentum in the x direction. If x is "left" and "right" then we are thinking about momentum going from left to right entering the point from the right and exiting the point to the right. Again, that momentum can be photons or any other quantum field content.
T_0i and T_i0 can be thought of momentum-energy which originates or terminates at the point, arriving or departing in the i direction; more precisely, if you know some special relativity, T_00 here looks like \gamma m_0 c^2 and T_0i looks like \gamma m_0 \vec{v}_{i} c.
For completeness, the non-diagonals, T_ij, i,j ! =0, i != j are the fluxes of i momentum the j direction, or equivalently with our choices, the total momentum times the velocity in the j direction.
So, considering the middle space of three 3d spaces at time coordinates t-1, t, and t+1, at a point p the stress-energy tensor T encodes the all the quantum field values and changes thereof that contribute to the energy-momentum that is constant at p (in T_00) or which arrive and depart p in the three spacelike directions. The momentum is deposited into the "matter" at the point and adjacent (but in the future light cone) points in spacetime we are looking at, and arrives from the matter the adjacent points in spacetime in the past light cone. [4]
When taking this sort of semiclassical approach we usually write G = <T> where the angle ...
I'm way outside my wheelhouse here for knowing what the standard model allows so please bear with me.
It's what I get for my drive-by commenting :)
Now I wish I'd omitted the "but I could be wrong" so I'd have looked a bit more decisive — and, y'know, less guarded-because-I've-been-on-forums-long-enough-to-know-that-I-should-cover-my-ass-against-all-possible-scenarios.
http://norbert-winter.com/wp-content/uploads/2018/02/2017-03...
1) 1.1, 1.2 does not contain a dimensionful coupling constant
2) It contains the point-split which Heisenbergs equation is lacking of.
Edit/post script: I also don't see that the word "algebra" is mentioned in the document at all. By comparison the Wikipedia page on spinors uses the word "algebra" 116 times. That seems odd if this theory is based on a deep understanding of spinors.
http://norbert-winter.com/wp-content/uploads/2018/02/2014-05...
I find the excessive use of "colossal" and "rupture" to be very suggestive of a Freudian slip implying the author is subconsciously aware that his inspiration followed a massive cerebral hemorrhage.
I'm not sure why you are promoting it if you can't explain it yourself.
Here, for comparison, is what appears to me to be a normal scientific paper that mentions spinors:
Supersymmetry, supergravity theories and the dual spinor model F Gliozzi, J Scherk, D Olive - Nuclear Physics B, 1977
http://cds.cern.ch/record/203097/files/CM-P00061869.pdf
Note that it does not end with "THE END" and it does cite other scientific works.
Your link reminds me of those manila envelopes. Cargo cult science indeed!
It's almost as if your question is being interpreted as either:
1) as defense of the manila envelope (how is a question a defense?)
2) as indicating you are the author of the envelope (that probability would be incredibly low!)
3) as being written by the same author who made some other unliked comment in this topic (since when do we downvote all comments of an author as soon as we dislike one of his comments?)
But downvoting in the first place seems reasonable.
Not trying to attack the standard model here but rather showing interest in discussing a new approach.
1. Not prepared with LaTeX. 2. Photo of the author. 3. Obsession with rounded rectangles and ovals. 4. It uses the word "colossal" 83 times and "rupture" 110 times. 5. Didn't see any references to other scientific works.
As an aside, I like the understated way the description is written:
The extraction of these events from the LHC data is challenging as there are many mundane type of events that can mimic them. Identifying these events requires measurements from all CMS subdetectors, which makes the reconstruction quite complex.
I can only imagine what the value of "many" and the amount of effort behind "challenging"and "quite complex" really is.
I'd choose looking over mundane data every day for that, regardless of how boring it was, if only to be in the shadow of giants.
(actually the phrasing was quite a bit funnier in Dutch: "huis- tuin- en keukenquantum")
I haven't looked too carefully at the CMS result, so no comment there.
However, in CMS we have recently started using Deep Neural Networks. These are used for the separation of signal and background events in the "single-lepton channel" of the search, i.e., the search where the Higgs boson decays to two bottom quarks and the top quarks decay in such a way that at least one electron or muon is present in the final state. Again, more details here: [2]
[1] http://arxiv.org/abs/1803.05485
[2] http://cms-results.web.cern.ch/cms-results/public-results/pr...