Which lattice QCD calculations should I believe?
Matt Austern
are some major pitfalls to watch out for (e.g., how do you handle
dynamical fermions), but not enough to be able to tell, when I read a
paper from someone who's done one of the massive calculations on a
supercomputer, whether or not they have successfully avoided the
pitfalls. Nor do I know enough to be able to tell whether or not
people are engaging in wishful thinking when they report their error
estimates.
I've been especially worried after seeing one talk where someone doing
these calculations reported that he added extra terms to his action
that vanished in the continuum limit, and that these improved the
convergence properties of his calculation; it seems to me, though,
that if you use two different actions that differ only by terms that
vanish in the continuum limit and you end up getting two different
answers, this suggests that you might not have finite-size effects
under as much control as you thought you did.
My question, then, to anyone who really does know the field well:
which of these calculations (if any) do you regard as trustworthy,
and, in your opinion, how seriously should I take the results?
Thanks in advance!
--
Matthew Austern Maybe we can eventually make language a
ma...@physics.berkeley.edu complete impediment to understanding.
Paul Padley
lattice QCD calculations that I should believe". I am
so far unaware of any useful prediction that has ever been
made by a lattice QCD calculation. I would
like to hear of some examples otherwise.
Paul Padley
pad...@floyd.triumf.ca
Greg Kilcup
getting the bugs worked out of the moderation system. Correspondence should
go to Greg Kilcup rather than to me. -- MWJ.]
ma...@physics2.berkeley.edu (Matt Austern) listened to a seminar
on lattice gauge theory calculations, and came away asking ...
> which of these calculations (if any) do you regard as trustworthy,
> and, in your opinion, how seriously should I take the results?
That is easy to answer: (a) trust ours (b) take them very seriously (:-)
But seriously ...
Concerning "pitfalls" such as the lack of dynamical fermions, you
are certainly allowed to ask a seminar speaker about all the
possible sources of systematic error. There are rather few
calculations where people have addressed each possible source
quantitatively. But you shouldn't disbelieve the speaker when
he says the uncalculated errors are probably small; I trust most
of my colleagues to give straightforward answers.
To be concrete about it, a given lattice calculation is
characterized by the following set of parameters
*V* -- the lattice volume, or number of points in your grid,
typically 32^4 or smaller.
*a* -- the lattice spacing (controlled by the bare coupling *g*),
typically about .1 Fermi with a factor of 2 either way
*mq* -- the quark masses, typically about the strange quark mass
*Nf* -- the number of dynamical flavor, typically 0 ("quenched"),
since it is very expensive to include.
*N* -- the number of statistically independent measurements,
typically 100 or less.
The output is some number F(V,a,mq,Nf,N). We want to evaluate
this function in the limit (V --> infty, a --> 0, mq --> 0,
Nf --> 3, N --> infty), which is of course impossible on a
finite computer. However, one can do calculations to see how
much each parameter affects a given observable quantity.
One noteable (:-) set of calculations along these lines took
us a couple of years to assemble. Beginning from a completely
inadequate (IMHO) system with (V=16^3x24, a=.1F, mq=.5*mstrange,
Nf=0, N=35) we repeated the calculation of a particular quantity
of interest on a set of lattices with exactly the same parameters,
except that (a) in one the volume was increase to 24^3x40, and
(b) in another the spacing was decreased by a factor 2 while
the number of points went up by 2^4 (i.e. same physical volume),
and (c) in another we added dynamical fermions. This let us
state with confidence that we know the answer to within a few
percent, barring some bizarre coincidence. There are a couple
of other groups who have put in a similar amount of effort so
as to reduce the amount of handwaving they have to do in seminars.
Concerning statistical errors, it has taken a few years for
standard statistical techniques to percolate through the lattice
community, but nowadays you have every right to demand that
your speaker be familiar with the following terms: (correlation
matrix, singular value decomposition, jackknife, and bootstrap).
If these are applied, the statistical errors should actually
be meaningful. That is, if the same person redoes the exact
calculation with a new random number generator, 2/3 of the time
his new number will lie within the previously stated errors.
Still there is a (maybe not so) hidden source of systematic
error coming from the choice of the data to include in a fit.
Thus different groups doing what seems to be the same calculation
will in fact sometimes offer two numbers outside the mutual
statistical errors. One of my current research projects is to
clean this situation up, and I have recently been punishing
myself with books by real statisticians; there are three
on my desk at the moment in fact.
Finally, concerning your seminar speaker's addition of terms
to his action, that is a very good idea which has become rather
prominent in the last couple of years. You are of course
right that if I have two functions f(a) and g(a) which are
supposed to give the same physical quantity in the continuum
limit, then I had better hope that f(a=0) = g(a=0). But it
may well be that g(a) is more weakly dependent on *a* than
is f(a). Then it makes a lot more sense to try to extrapolate
to a=0 using g(a). That is the whole idea behind improved actions.
---------------------------------------------------------------
Greg Kilcup kil...@pacific.mps.ohio-state.edu
Asst. Prof. of Physics kil...@ohstpy.bitnet
The Ohio State University (614) 292-3224
---------------------------------------------------------------
--
Bill Johnson | My suggestion for an Official
Los Alamos National Laboratory | Usenet Motto: "If you have nothing
Los Alamos, New Mexico USA | to say, then come on in, this is the
!cmcl2!lanl!mwj (m...@lanl.gov) | place for you, tell us all about it!"
U16072%uic...@ohstvma.acs.ohio-state.edu
Austern) says:
>I've been especially worried after seeing one talk where someone doing
>these calculations reported that he added extra terms to his action
>that vanished in the continuum limit, and that these improved the
>convergence properties of his calculation; it seems to me, though,
>that if you use two different actions that differ only by terms that
>vanish in the continuum limit and you end up getting two different
>answers, this suggests that you might not have finite-size effects
>under as much control as you thought you did.
I'm not a lattice gauge person so I can only give you an idea of the
correct concepts. About the way to judge results, I feel the same
way about experimental talk ( being a field theorist ).
When you are on a lattice and you take the continuum limit, correlation
functions (aka matrix elements) go like exp(-chi|x|/a) where a is the lattice
spacing and chi is the "correlation" length, and a is the lattice spacing.
For the actual limit a->0 so that the correlation functions become trivial .
unless chi=0. For this to happen you must be at a critical point of the theory.
The difficulty with this is that at criticallity you must have scaling.
Or the masses and the couplings must be zero (too simple technical detail here)
To avoid this you set the coupling call it g to zero as a goes to zero.
Redefine g as g'=g/a^some number, hold g' fixed as a->0. Then g' becomes
the new coupling. In essence as you approach the continuum limit you
perturb by an amount that goes to 0. This has an fancy name, renormalisation.
In essence you are choosing a path to approach where the values make sense
and the theory makes sense. This is similar to finding the greens function
of the wave eqn in E&M by contour integration. You have to resort to
causality to determine which particular cut to choose (at times you have to
make choices such as whether to keep gauge invariance or chiral symmetry).
The term that leads to better convergence just seems to be a different way
to approach the continuum limit.A decent review is Tom DeGrand in
"From Actions to Answers", 1989 TASI lectures, World Scientific.
--------------------------------------------------
Thaddeus Olczyk, University of Illinois at Chicago
olc...@uicws.phy.uic.edu
SCOTT I CHASE
>I would like to rephrase the question to, "are there any
>lattice QCD calculations that I should believe". I am
>so far unaware of any useful prediction that has ever been
>made by a lattice QCD calculation. I would
>like to hear of some examples otherwise.
If by "useful" you mean "suggestive," then I would say that there
are at least a few such results. There is general concensus (with
some notable exceptions) that lattice QCD indicates the presence
of a phase transition from hadronic to quark matter for certain
experimental conditions, such as high energy density (~3-10 GeV/fm^3),
low baryon chemical potential, etc. These "observations" are
suggestive and useful for designing the best possible experiments
for finding signatures for quark deconfinement.
Lattice calculations are also useful for making rough characterizations
of, for example, the glue-ball and high-glue-content hadron mass spectra,
which then motivates experiments of specific types.
Whether there are any calculations which are good enough to be
"useful" in the sense of "useful in testing the predictions of QCD"
is another matter altogether - in this case I would tend to agree
that good examples would be difficult to find. Only if we are fortunate,
for example, to find evidence for a deconfinement phase transition
under the conditions estimated by lattice gauge calculations would we
then say in retrospect that the lattice calculations were "useful"
in this sense - we would have extracted an experimentally verified
semi-quantitative prediction of non-perturbative QCD.
-Scott
--------------------
Scott I. Chase "It is not a simple life to be a single cell,
SIC...@CSA2.LBL.GOV although I have no right to say so, having
been a single cell so long ago myself that I
have no memory at all of that stage of my
life." - Lewis Thomas
(Xavier Llobet EPFL - CRPP 1015 Lausanne CH)
>I've been especially worried after seeing one talk where someone doing
>these calculations reported that he added extra terms to his action
>that vanished in the continuum limit, and that these improved the
>convergence properties of his calculation; it seems to me, though,
>that if you use two different actions that differ only by terms that
>vanish in the continuum limit and you end up getting two different
>answers, this suggests that you might not have finite-size effects
>under as much control as you thought you did.
>
to the _same_ result, but at different rates. If we want to compute
Sum(k=1,k=inf) 1/(4 k^2 - 1)
we may add
(1 - 4 k (k-1))/(4 k^2 - 1)^2
to each term, and the convergence improves by one order, from O(1/k) to
O(1/k^2). In a situation involving a mesh size, you may similarly have two
expressions which converge to the same result as the mesh decreases to zero,
but at different rates. For example, if you have to evaluate the first
derivative of u(x) in a mesh of size h, you may do it as
(u(x+h) - u(x-h))/2h (error in h^2)
or
(-u(x+2h)+8u(x+h)-8u(x-h)+u(x-2h))/12h (error in h^4)
>My question, then, to anyone who really does know the field well:
>which of these calculations (if any) do you regard as trustworthy,
>and, in your opinion, how seriously should I take the results?
I don't know this field at all, but the above example appears to me quite
general. The convergence of numerical calculations is an enormous open field
of research in itself; I do not pretend to be a specialist, so do not take the
examples above too literally.
>
>Thanks in advance!
>--
>Matthew Austern Maybe we can eventually make language a
>ma...@physics.berkeley.edu complete impediment to understanding.
>
-xavier
Matt Austern
> These two things are different! You may have two series, both converging
> to the _same_ result, but at different rates. If we want to compute
>
> Sum(k=1,k=inf) 1/(4 k^2 - 1)
>
> we may add
>
> (1 - 4 k (k-1))/(4 k^2 - 1)^2
>
> to each term, and the convergence improves by one order, from O(1/k) to
> O(1/k^2). In a situation involving a mesh size, you may similarly have two
> expressions which converge to the same result as the mesh decreases to zero,
> but at different rates. For example, if you have to evaluate the first
> derivative of u(x) in a mesh of size h, you may do it as
>
> (u(x+h) - u(x-h))/2h (error in h^2)
>
> or
>
> (-u(x+2h)+8u(x+h)-8u(x-h)+u(x-2h))/12h (error in h^4)
That's true, and I was perhaps unclear in my original post, so let me
take this opportunity to clarify.
If your action is originally S[A,a], and you alter it by adding a term
S1[A,a], where S1 vanishes in the continuum limit, then you're
essentially adding a free parameter to the model: the coefficient of
S1.
Now, this might sound really stupid, but it's not clear to me how you
would prove that your new action, S+S1, really converges faster than S
does. After all, you can always tune the coefficient of S1 so that
your prediction for whatever quantity you're looking at (m_pi/m_rho,
let's say) is better, so how do you make sure that what you have
really is an action that converges better, instead of an action that
converges just as slowly but that has been fit to some experimentally
measured quantity?
I'm sure that the people who actually do this have worried about this
question, and I'm sure that they do have ways of showing that their
improved actions really do have better convergence properties---I just
don't know enough to be able to tell, from their papers, what they're
doing.
In any case, I don't really want to focus so much on this one
question: it's just one of several technical details in lattice
calculations that I don't understand. (And, I might add: for every
tricky technical detail that I'm aware of, I'm sure there are ten more
that I'm not aware of.)
The point is just that I'm sure some of these lattice calculations are
better than others, and I find it a bit frustrating that I'm not
really able to tell, from reading a paper describing a calculation,
how seriously I ought to take it.
Greg Kilcup
In response to ma...@physics2.berkeley.edu (Matt Austern)'s original
question, Paul Padley <pad...@floyd.triumf.ca> chimes in with ...
> I am so far unaware of any useful prediction that has
> ever been made by a lattice QCD calculation.
sic...@csa3.lbl.gov (SCOTT I CHASE) finds some qualitative
use for lattice QCD, but as far as really useful things, he
> ... would tend to agree that good examples would be difficult to find.
In response, I say ...
OUCH! You sure know how to make a guy feel good about his work! (:-)
Anyway, I would suggest that lattice QCD has become quite useful
in the last few years, but I would like to distinguish three possible
meanings of "useful". First there is the motivation to understand QCD
for its own sake, and make sure it really is the correct theory of hadrons.
Secondly, there is the motivation to understand details of hadronic
structure which may not be well determined by experiment at the
present time. These first two categories are really the same thing,
but we are distinguishing pre-dictions from post-dictions, on the
grounds that a prediction may be "useful" for an experimenter. Finally,
there is the motivation to study the weak (or GUT-scale) interations of
quarks, in which case QCD is an annoying "background" to be removed.
I will argue that lattice QCD is useful in all three senses.
As one tired, overworked example in the first category of usefulness,
lattice QCD has produced numbers for the spectrum of light hadrons,
i.e. the masses of the proton, rho etc. In the last year the precision
has come down to about the 5% level. This may not seem fantastically
useful, since we already know the mass of the proton, and everyone believes
that QCD should predict these numbers. But then again, what other
non-lattice means do we have to do an honest, first-principles
calculation in QCD? So I would say this is as useful as the solution of
the Schroedinger equation is for the hydrogen atom.
In the second category I would put some of the things Scott mentioned,
e.g. glueball masses, the quark-gluon phase transition temperature etc.
These are things which experimenters might measure in the next few
years, and for which 5-10% accuracy is plenty. Other quantities in
this category would be various details of hadronic structure, such
as the determination of the spin content of the proton, the "sigma term",
and certain form factors, including a magnetic moment or two which have
not been measured yet. Also on this list would be the determination
of the strong coupling constant alpha_s, or equivalently the scale
parameter Lambda_QCD. The lattice number is already as precise as the
determination from jet production at LEP, and will quickly improve.
Finally, lattice QCD has become *extremely* useful in the study of weak
interactions. Here one has experimental data (well at least some data) and
want to extract from that the various coupling constants between quarks
and W bosons. This information will both tidy up the Standard Model, and
hopefully give some clues as to what lies beyond. The obstacle is that
the quarks always appear in the form fo nonpeturbative bound states, and
there is some nontrivial hadronic matrix element to compute. On dimensional
grounds, or on the basis of models, one can typically estimate the matrix
element to within a factor of two or three. But that is not good enough
to be useful. For a variety of matrix element, lattice QCD now gives
results at the 10-15% level or better. This is the best we've got from
any source, and enables us to say something quantitative about the
Cabbibo-Kobayashi-Maskawa matrix.
There are a variety of reasons why it may seem to the outsider that
lattice QCD hasn't produced much, including (1) because progress is gradual,
(2) because we have grown used to the idea that QCD is the correct
theory of the world, so we are completely unsurprised by things like
the calculation of the QCD spectrum, or (3) it seems that there are
other methods of calculation which are easier and as accurate.
In the latter category I have in mind the naive nonrelativistic
quark model and its cousins, which work about as well as lattice QCD
for many quantities. However, the reasons for its success are still
utterly mysterious, and in some cases (e.g. the proton spin) it fails
completely. The situation here is somewhat similar to the beginnings
of quantum mechanics, when Bohr's theory already gave the Balmer spectrum
for reasons which in retrospect seem almost accidental. In the same way
one should always bear in mind that in contrast to the models, lattice QCD
is an actual first-principles *theory*, with no fudge factors.
Lastly, I have appended a list of various quantities which have been
looked at on the lattice, dividing them along the lines indicated above.
=========================
| QCD for QCD's sake |
=========================
light hadron spectrum: proton, rho, delta, ...
glueball spectrum
topological susceptibility
magnetic moments
EM form factors
wavefunctions
sigma term
spin content of proton
transition to quark-gluon plasma
charmonium, upsilon spectrum
determination of alpha_strong
===============================================
| QCD for the sake of Weak Interactions etc. |
===============================================
B_K, B_B
epsilon-prime
f_B
D->K,K* form factors
proton decay matrix elements
Matt Austern
> As one tired, overworked example in the first category of usefulness,
> lattice QCD has produced numbers for the spectrum of light hadrons,
> i.e. the masses of the proton, rho etc. In the last year the precision
> has come down to about the 5% level. This may not seem fantastically
> useful, since we already know the mass of the proton, and everyone believes
> that QCD should predict these numbers.
That's impressive! I didn't realize that lattice results were
anywhere near that level of accuracy. (In fact, to be honest, I
hadn't realized that anyone was able to calculate anything in QCD,
either in the perturbative or the nonperturabative regime, to better
than 10% or so.)
I'm surprised that these results didn't get more publicity when they
came out. Have the papers on this work been published yet?
John F. Donoghue
> In article <KILCUP.93F...@pacific.mps.ohio-state.edu>
kil...@pacific.mps.ohio-state.edu (Greg Kilcup) writes:
> > As one tired, overworked example in the first category of usefulness,
> > lattice QCD has produced numbers for the spectrum of light hadrons,
> > i.e. the masses of the proton, rho etc. In the last year the precision
> > has come down to about the 5% level.
> That's impressive! I didn't realize that lattice results were
> anywhere near that level of accuracy.
It seems to me that the group at Fermilab has done some calculations which
purport to give the strong coupling constant \alpha_s(m_c) by comparing
the lattice charmonium spectrum with experimental data. I don't know
the details, but the authors would probably include A. Kronfeld and/or
A. El Khadra.
hans.dykstra
abp...@deimos.ucc.umass.edu
[Moderator's note: I have taken the liberty of trimming down the quotes
of earlier posts. I would recommend maximizing the ratio of new/old
information subject to the constraint of intelligibility.]
Christoph Best
In article <AUSTERN.93...@beauty5.lbl.gov>, aus...@beauty5.lbl.gov (Matt Austern) writes:
|>
|> If your action is originally S[A,a], and you alter it by adding a term
|> S1[A,a], where S1 vanishes in the continuum limit, then you're
|> essentially adding a free parameter to the model: the coefficient of
|> S1.
|>
|> Now, this might sound really stupid, but it's not clear to me how you
|> would prove that your new action, S+S1, really converges faster than S
|> does. After all, you can always tune the coefficient of S1 so that
|> your prediction for whatever quantity you're looking at (m_pi/m_rho,
|> let's say) is better, so how do you make sure that what you have
|> really is an action that converges better, instead of an action that
|> converges just as slowly but that has been fit to some experimentally
|> measured quantity?
I am also just getting into the subject of lattice QCD, so I hope I can contribute
from my own misunderstandings:
As far as I understand, the continuum action is not a well-defined entity
because the integration measure in the path integral is unknown, at least
for realistic theories. The lattice action, on the contrary, is well defined
but it is not easy to show what happens in the continuum limit a->0. The
naive continuum limit just provides a first guess by showing that the
continuum limit of the _action_ gives the continuum action. Observables
like correlation function might still diverge and must be renormalized
before their continuum limit can be taken.
Formally, this is expressed by the renormalization group which describes
how observable quantities change when the lattice spacing and the parameters
of the action are changed. To take the lattice spacing to zero, one has
to find a fixed point where a change in the lattice spacing can be
compensated by a change in some parameter (like the charge).
So the procedure to investigate a given lattice action is to find out the
renormalization group equations (RGE) for some observable quantities using
this action and see if there is a fixed point. At the fixed point, continuum
observables can be computed which do not depend on the lattice spacing.
These observables will in some way not feel the influence of the finite
lattice spacing. One says, they exhibit universality. The question is: Do
they feel the difference between a lattice action S and another S+S1.
Luckily, even if I do not exactly understand how, one can classify operators
(i.e. actions) according to their relevance to the continuum limit. It
turns out that the properties of a theory at a fixed point do not depend
on the coefficients of certain operators in the action, and this is why
people seem so sure about being able to modify the lattice action. The
influence of these operators is, in some way, proportional to the lattice
spacing and goes to zero in the continuum limit. The operators that
survive have values that, whence scaled by the lattice spacing, diverge.
In particular, the correlation length of a theory, expressed in terms of
the lattice spacing, must diverge to exhibit any correlations in the
continuum limit! This is why the continuum limit can be taken at a phase
transition.
So if two lattice theories with two different actions give different answers,
the difference is due to out inability to have large enough lattices. If
the lattice spacing were fine enough, the difference due to irrelevant
operators should vanish, or something is wrong either with the calculations
or the renormalization group.
One point I have always found hard to get is this: Nonabelian gauge theories
are asymptotically free. This means, at very _small_ lattice spacings one
can use perturbation theory. So the lattice people do not need to make their
lattices arbitrarily small, they just want to make it so small that
perturbation theory is valid. Then they can use perturbative predictions
to extrapolate to the continuum. On the other side, the total volume of
the lattice should be large enough that a nucleon can fit in it which
seems to be the real problem.
I would also like to mention that for other theories it is not at all
clear which lattice action is correct. For QED, there is compact QED
which seems to have unphysical properties (?), and noncompact QED. Last
not least, some theories which seem perfectly right in perturbative
renormalization probably have vanishing interaction in the continuum
limit, like the phi^4 theory in more than 4 dimensions.
--
Christoph Best | Sex is the mathematics
cb...@th.physik.uni-frankfurt.de | urge sublimated.
| -- M. C. Reed.