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    More Confirmations On Y(4140) And Y(4270) From BaBar
    By Tommaso Dorigo | February 24th 2014 05:07 AM | 10 comments | Print | E-mail | Track Comments
    About Tommaso

    I am an experimental particle physicist working with the CMS experiment at CERN. In my spare time I play chess, abuse the piano, and aim my dobson...

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    The Y(4140) state, a resonance found in decays of the B meson to J/ψ φ K final states, is the protagonist of a long saga. Originally it was obseved by CDF in 4 inverse femtobarns of Run 2 data by Kai Yi, a very active "bump hunter" in the experiment - and I want to add, a successful one! 

    Kai had to withstand a very long review process within the collaboration before the evidence for the new particle could finally be published; and the addition of more data to the analysis, one year afterwards, left many in CDF with the suspect that the particle was maybe there only in the eye of the beholder: the new data did not seem to show a clear hint of the peak seen in the first part.

    Despite that, CDF ended up publishing the result of the full analysis, which -when the background was fit with a more "physics motivated" and less conservative function- yielded a larger statistical significance for the observed effect. It was a somewhat controversial situation.

    After the publication by CDF, many experiments produced searches for the structure. While CMS soon showed a confirming signal in its data, and hints of a second resonance some 130 MeV more massive, the LHCb collaboration denied the presence of the signals. DZERO later confirmed the CDF find.

    Overall the picture could have been more clear with four experiments carefully looking at similar data, and some have continued to speculate that the structures are not particles but deformations of the kinematical distributions of the bodies produced in B hadron decays, due to non-well-understood dynamical effects. To me, the Y(4140) and Y(4270) look like well-established resonances, and I do not understand the objections, although maybe I am just being a bit naive. The most interesting thing to me remains that LHCb, which of the four above experiments is the one allegedly better equipped to do B physics, is the one which has failed to see anything; it looks as if the anomaly is in the LHCb field now...

    In the meantime another B physics dedicated experiment, BaBar, has looked for the Y states in its data sample, and has found results which are still open to different interpretations; but again I take them as a further positive confirmation of the original CDF signal.

    The mass distribution extracted by BaBar is shown on the right. As usual, black points are experimental data; the red curve is the interpretation which includes the two structures, while the blue curve is a background-only model. As you can see, a fit which includes the two resonant structures is a much better model of the data than a simple "phase space" potato-like distribution.

    Note that in the above graph BaBar histograms the squared mass, for reasons that I will not explain here. Also note that Babar uses the reproachable habit of plotting sqrt(N) error bars on their data. This is IMO deceiving, and frankly very unfortunate. Let me turn the diatriba mode on in the next paragraph to explain what I mean.

    Diatriba mode on

    When one chooses to plot a point with an error bar in a histogram representing event counts, one is plotting two things at once, whether one knows it or not. In each bin, the point shows both the observed event counts -a number with no error- and the Maximum Likelihood Estimate (MLE) for the Poisson mean μ of the process that has yielded those counts in that bin. The two are coincident.

    Note that the former has no error. The latter does, and so one can proceed to attach an error bar to the point. I stress that the bar is of course relevant to the MLE, not the observed count which, I repeat, has no error. So this error bars is supposed to represent a range of possible values for the Poisson mean μ. Since in the absence of a specification the error bar is supposed to "cover" 68% of the possible values (as the integral of a Gaussian between -1σ and +1σ), that is what we expect the bars to do in the graph. But they do not ! In situations with very small event counts, an error bar from "μ-sqrt(μ)" and "μ+sqrt(μ)" as plotted above has very bad coverage properties. In other words, the bar represent a much smaller variation of possible μ values than what authors imply. Not 68% but in some cases much less.

    The solution, due to Garwood, is 80 years old. It is to plot "central" asymmetric error bars which correctly cover at 68%. These are extracted by a simple rule by the inversion of the so-called "Neyman construction". Leaving that detail aside, it is very annoying to see otherwise respected particle physics experiments letting go with these perfectible graphs.

    If you think this is a arguable detail think better: those error bars are there for a purpose, and they should not be deceiving. In particular, when one overlays a maximum likelihood fit to the points, the eye of the "user" will instinctively compare the curve with how much the points scatter around it. Error bars that undercover will lead the user to conclude that the fit is a poor one - but the fit used the Poisson distribution of the data, not the Gaussian approximation sqrt(N) ! Take e.g. the point at abscissa 19 in the graph below: it seems like it is 3- or 4-standard deviations away from the red fit, but a correct-coverage error bar would have made it clear that the disagreement is not large.

    If you think that asymmetric error bars "confuse the user", you are deluded. We routinely publish confidence intervals in our HEP results, and now in a histogram we should "protect the user" who, poor soul, would get confused by a non-sqrt(N) error bar ? Come on. Fix those error bars, BaBar friends !

    Back to the Y states

    If they size up the signals, they come up with the following estimates for the fraction of "resonant" contributions: f(4140) = 7.3%, f(4270)=7.7%. Both estimates come with a largish error, respectively 4.5% and 6.4% (where I have combined statistical and systematical errors). Let us look also at the other experiments: they find

    exp     Y(4140) fraction / Y(4270 fraction)
    ----------------------------------------------------
    CDF:   14.9+-3.8%       /    N/A
    DZERO:     19+-8%      /    N/A
    CMS:    13.4+-3%        /   18.0+-7.3%
    LHCb:      < 7%            /     < 8%

    (Disclaimer of liability: Note that I am relying on information from a talk by Elisa Fioravanti at Lake Louise, here; the CMS numbers are her estimates and I take no responsibility for those numbers - in fact I am too lazy today to go and check them).

    Excluding LHCb, it seems as if the Y(4140) is a well-established structure appearing in a 14% fraction of the decays, and the Y(4270) is no less solid, and it appears in a similar fraction of the decays. Including LHCb, the five datasets appear slightly inconsistent, although not enough to doubt that the structures are real. That is at least my very personal interpretation of the state of matters.

    Comments

    Tommaso -- I am aware that your very astute criticisms of the Babar presentation plots have been communicated to the Babar analysts, who will now hopefully ameliorate them. Thanks.

    dorigo
    That's great news ! Thanks Anon.
    T.
    dorigo
    Ah - and: in that case please be sure to let them know that the "standard" way of plotting asymmetric error bars in root fails for zero-entry bins. The upper limit of the error bar for a bin
    with zero entries should go all the way to 1.8 or so, and not to 1.25 as the default in RooFit
    will do.
    The recipe to do the right thing is as shown below:

    void PrintGarwood (int imax=10) {
       const double alpha = 1 - 0.6827;
    //   TH1D * h1 = new TH1D("h1","h1",50,-4,4);
    //   h1->FillRandom("gaus",100); 
    //    TGraphAsymmErrors * g = new TGraphAsymmErrors(h1);
    //    g->SetMarkerSize(0.5);
    //    g->SetMarkerStyle (20);

        for (int i = 0; i < imax ; ++i)  {    
    // for (int i=0; i < g->GetN(); ++i) {
           int N = i; // g->GetY()[i];
           double L =  (N==0) ? 0  : (ROOT::Math::gamma_quantile(alpha/2,N,1.));
           double U =  ROOT::Math::gamma_quantile_c(alpha/2,N+1,1) ;
           cout << "N= " << i << ": low = " << L << " up = " << U << endl;
    //       g->SetPointEYlow(i, N-L);
    //       g->SetPointEYhigh(i, U-N);
       }
    //   g->Draw("AP");
    }


    Cheers,
    T.
    To me, the Y(4140) and Y(4270) look like well-established resonances, and I do not understand the objections, although maybe I am just being a bit naive.

    Yes you are. Let me explain why.

    A vast number of three-body decays of heavy (and light) hadrons have been studied experimentally. I am not aware of a single example where the decay products follow a simple phase-space distribution. This is not surprising -- the strong interaction induces complicated hadronic effects, as we all know.

    As clearly shown by CDF, CMS and others, the distribution of events in B+ -> J/psi phi K+ decays does not follow phase-space. This is not argued by anyone, nor is it in the least surprising. The question is whether or not the structures seen in the J/psi phi invariant mass are due to resonances or not (and only if they are is it appropriate to refer to them as X(4140), X(4270), etc.). As a statistics expert you know how to answer this question: hypothesis testing. Specifically, we need to compare the likelihood of the (null) hypothesis that the structures are not caused by resonances with that in the case that resonances are included.

    None of the experimental results to date have addressed this satisfactorily (or at all). Instead, what has been done is to take the null hypothesis as being a phase-space distribution. As explained above, this is not appropriate. The only way to address properly the question of whether or not there are resonances in J/psi phi is with a detailed analysis of the full distributions of the decays across phase-space -- which will be very complicated indeed, so you will have to be patient.

    [There is a caveat -- in case a resonance is very narrow, with width of, say, 10 MeV or less -- one can assume that any other contributions are phase-space-like in the region under the peak. This was the case for the first CDF claim on the X(4140), but later data show that the structure is much wider. So unfortunately this shortcut is not possible.]

    Ultimately, what it boils down to is that it is not sufficient to say "these peaks look like resonances" -- we need rigorous scientific proof, and we do not have it, yet. It may turn out that they are due to exotic states, which would be very exciting. On the other hand, you do not need to look too far into the literature to find examples of claimed peaks that turned out to be spurious.

    Cheers
    Tim

    dorigo
    Thanks for your comment Tim. Yes, I know the argument, but I saved my audience from those complications above (actually a similar discussion to this one arose in a former post on the Y(4140) in this very blog - I will now go back to see if I can find it).

    I agree that for the Y resonances to be established as real particles we need to know more of the dynamics of the decay; but in the absence of more detailed studies, I put my money there - I think they are indeed new states. Besides, when one does not know how the background behaves one usually tries different possibilities that "look reasonable", and takes the worst Z value as a hunch of the significance. This has been done in the first CDF analysis. The CMS result for the Y(4140) really can hardly be interpreted otherwise.

    On the other hand I well know that many earlier states have been found to be spurious, so yours is a perfectly legitimate point of view. What would convince everybody would be to produce these particles by themselves, if it is possible...

    Cheers,
    T.
    Dear Tomaso, the Y(4140) is definitively not well estabilished anywhere, except in the analyses performed from only one postdoc (in both project, CDF _and_ CMS). What do you expect, if you analyze the invariant mass of a 2-vector system, is it PHSP distributed, in your opinion? The BaBar data showed _only_ that the invariant mass system of J/psi-phi is not PHSP. This is somehow expected. The BaBar publication will follow soon, hopefully.

    ..and I wish to add one sentence: without a Dalitz plot analysis, nobody can conclude on that. The 2 experiments which are more strong in claiming the presence of Y(4140) and Y(4270) analyzed only J/psi to mumu, and only B+. Nobody knows about polarization effects of those 2 vectors, as well as I know (talking here of J/psi and phi). Nobody has a dedicated model for that. We can compare the J/psi-phi mass distribution only with PHSP, which is not appropiate at all in this analysis. I do not see that BaBar confirmed anything, here.

    dorigo
    What do you mean, one post-doc ? These analyses belong to the collaborations that approved them. The strength of your arguments has been nullified by your defamatory statement. Show your real name if you wish to continue this discussion.

    Cheers,
    T.
    Dear Tommaso,
    about the story of Y(4140) and Y(4270) I am still a bit puzzled. This plot from BaBar that here you show, taken from a confence talk, I assume, the one here that you point out, I would say: let's wait for the new BaBar paper, and then we can compare official approved numbers to the ones of the other experiments, and come up to conclusions.

    Dear Tommaso et all,
    finally the plot from the BaBar collaboration is shown at a conference. I'm looking forward to read the paper. Hopefully it will be published soon! Then, I could write here with my personal interpretation of the new Y states. I haven't all information to judge it, right now.

    Lena