Friday, December 23, 2011


Subject: Re: Update on response to Douglass et al.
Date: Thu, 10 Jan 2008 08:40:28 -0500
Cc: Tom Wigley <>, Karl Taylor <>, Thomas R Karl <>, John Lanzante <>, carl mears <>, "David C. Bader" <>, "'Francis W. Zwiers'" <>, Frank Wentz <>, Leopold Haimberger <>, Melissa Free <>, "Michael C. MacCracken" <>, "'Philip D. Jones'" <>, Steven Sherwood <>, Steve Klein <>, 'Susan Solomon' <>, "Thorne, Peter" <>, Tim Osborn <>, Gavin Schmidt <>, "Hack, James J." <>

Dear Ben,

Thank you for this detailed update of your work. A few thoughts for
your consideration ...

Where to submit this: Although I understand your and Phil's
reluctance to try IJC, it seems to me that, despite the new work
presented, this is really a comment on Douglass et al. and so rightly
belongs in IJC. If you suspect the review and publication process
there is unacceptably long, perhaps this should be confirmed by
inquiring with the editor, as a professional courtesy. Decide in
advance what you'd consider a reasonable turn-around time, and if the
editor says it will take longer, going with another journal makes

Figures: They look great. As usual, you've done a super job telling
the story in pictures. One suggestion would be to indicate in Fig. 3
which test, or trio of tests, is the most appropriate. Now it is shown
as the blue curves, but I'd suggest making these black (and the black
ones blue) and thicker than the rest. That way those readers who just
skim the paper and look at the figures will get the message quickly.

Observations: Have you considered including results from HadAT and
RATPAC as well as RAOBCOR? For even greater completeness, a version
of RATPAC pared down based on the results of Randel and Wu could be
added, as could Steve Sherwood's adjusted radiosonde data. I'd
suggest adding results from these datasets to your Fig. 1, not the
planned Fig 4, which I gather is meant to show the differences in
versions of RAOBCOR and the impact of Douglass et al.'s choice to use
and early version.

With best wishes,

----- Original Message -----
From: Ben Santer <>
Date: Wednesday, January 9, 2008 10:52 pm
Subject: Update on response to Douglass et al.

> Dear folks,
> I just wanted to update you on my progress in formulating a
> response to
> the Douglass et al. paper in the International Journal of
> Climatology
> (IJC). There have been several developments.
> First, I contacted Science to gauge their level of interest in
> publishing a response to Douglass et al. I thought it was
> worthwhile to
> "test the water" before devoting a lot of time to the preparation
> of a
> manuscript for submission to Science. I spoke with Jesse Smith,
> who
> handles most of the climate-related papers at Science magazine.
> The bottom line is that, while Science is interested in this issue
> (particularly since Douglass et al. are casting doubt on the
> findings of
> the 2005 Santer et al. Science paper), Jesse Smith thought it was
> highly
> unlikely that Science would carry a rebuttal of work published in
> a
> different journal (IJC). Regretfully, I agree. Our response to
> Douglass
> et al. does not contain any fundamentally new science - although
> it does
> contain some new and interesting work (see below).
> It's an unfortunate situation. Singer is promoting the Douglass et
> al.
> paper as a startling "new scientific evidence", which undercuts
> the key
> conclusions of the IPCC and CCSP Reports. Christy is using the
> Douglass
> et al. paper to argue that his UAH group is uniquely positioned to
> perform "hard-nosed" and objective evaluation of model
> performance, and
> that it's dangerous to leave model evaluation in the hands of
> biased
> modelers. Much as I would like to see a high-profile rebuttal of
> Douglass et al. in a journal like Science or Nature, it's unlikely
> that
> either journal will publish such a rebuttal.
> So what are our options? Personally, I'd vote for GRL. I think
> that it
> is important to publish an expeditious response to the statistical
> flaws
> in Douglass et al. In theory, GRL should be able to give us the
> desired
> fast turnaround time. Would GRL accept our contribution, given
> that the
> Douglass et al. paper was published in IJC? I think they would -
> we've
> done a substantial amount of new work (see below), and can argue,
> with
> some justification, that our contribution is more than just a
> rebuttal
> of Douglass et al.
> Why not go for publication of a response in IJC? According to
> Phil, this
> option would probably take too long. I'd be interested to hear any
> other
> thoughts you might have on publication options.
> Now to the science (with a lower-case "s"). I'm appending three
> candidate Figures for a GRL paper. The first Figure was motivated
> by
> discussions I've had with Karl Taylor and Tom Wigley. It's an
> attempt to
> convey the differences between our method of comparing observed
> and
> simulated trends (panel A) and the approach used by Douglass et
> al.
> (panel B).
> In our method, we account for both statistical uncertainties in
> fitting
> least-squares linear trends to noisy, temporally-autocorrelated
> data and
> for the effects of internally-generated variability. As I've
> described
> in previous emails, we compare each of the 49 simulated T2 and
> T2LT
> trends (i.e., the same multi-model ensemble used in our 2005
> Science
> paper and in the 2006 CCSP Report) with observed T2 and T2LT
> trends
> obtained from the RSS and UAH groups. Our 2-sigma confidence
> intervals
> on the model and observed trends are estimated as in Santer et al.
> (2000). [Santer, B.D., T.M.L. Wigley, J.S. Boyle, D.J. Gaffen,
> J.J.
> Hnilo, D. Nychka, D.E. Parker, and K.E. Taylor, 2000: Statistical
> significance of trends and trend differences in layer-average
> atmospheric temperature time series, J. Geophys. Res., 105, 7337-
> The method that Santer et al. (2000) used to compute "adjusted"
> trend
> confidence intervals accounts for the fact that, after fitting a
> trend
> to T2 or T2LT data, the regression residuals are typically highly
> autocorrelated. If this autocorrelation is not accounted for, one
> could
> easily reach incorrect decisions on whether the trend in an
> individual
> time series is significantly different from zero, or whether two
> time
> series have significantly different trends. Santer et al. (2000)
> accounted for temporal autocorrelation effects by estimating r{1},
> the
> lag-1 autocorrelation of the regression residuals, using r{1} to
> calculate an effective sample size n{e}, and then using n{e} to
> determine an adjusted standard error of the least-squares linear
> trend.
> Panel A of Figure 1 shows the 2-sigma "adjusted" standard errors
> for
> each individual trend. Models with excessively large tropical
> variability (like FGOALS-g1.0 and GFDL-CM2.1) have large adjusted
> standard errors. Models with coarse-resolution OGCMs and low-
> amplitude
> ENSO variability (like the GISS-AOM) have smaller than observed
> adjusted
> standard errors. Neglect of volcanic forcing (i.e., absence of El
> Chichon and Pinatubo-induced temperature variability) can also
> contribute to smaller than observed standard errors, as in
> CCCma-CGCM3.1(T47).
> The dark and light grey bars in Panel A show (respectively) the 1-
> and
> 2-sigma standard errors for the RSS T2LT trend. As is visually
> obvious,
> 36 of the 49 model trends are within 1 standard error of the RSS
> trend,
> and 47 of the 49 model trends are within 2 standard errors of the
> trend.
> I've already explained our "paired trend test" procedure for
> calculating
> the statistical significance of the model-versus-observed trend
> differences. This involves the normalized trend difference d1:
> d1 = (b{O} - b{M}) / sqrt[ (s{bO})**2 + (s{bM})**2 ]
> where b{O} and b{M} represent any single pair of Observed and
> Modeled
> trends, with adjusted standard errors s{bO} and s{bM}.
> Under the assumption that d1 is normally distributed, values of d1
> >
> +1.96 or < -1.96 indicate observed-minus-model trend differences
> that
> are significant at some stipulated significance level, and one can
> easily calculate a p-value for each value of d1. These p-values
> for the
> 98 pairs of trend tests (49 involving UAH data and 49 involving
> data) are what we use for determining the total number of "hits",
> or
> rejections of the null hypothesis of no significant difference
> between
> modeled and observed trends. I note that each test is two-tailed,
> since
> we have no information a priori about the "direction" of the model
> trend
> (i.e., whether we expect the simulated trend to be significantly
> larger
> or smaller than observed).
> Stipulated sign. level No. of tests T2 "Hits" T2LT
> "Hits" 5% 49 x 2 (98) 2 (2.04%)
> 1 (1.02%)
> 10% 49 x 2 (98) 4 (4.08%) 2
> (2.04%)15% 49 x 2 (98) 7 (7.14%)
> 5 (5.10%)
> Now consider Panel B of Figure 1. It helps to clarify the
> differences
> between the Douglass et al. comparison of model and observed
> trends and
> our own comparison. The black horizontal line ("Multi-model mean
> trend")
> is the T2LT trend in the 19-model ensemble, calculated from model
> ensemble mean trends (the colored symbols). Douglass et al.'s
> "consistency criterion", sigma{SE}, is given by:
> sigma{SE} = sigma / sqrt(N - 1)
> where sigma is the standard deviation of the 19 ensemble-mean
> trends,
> and N is 19. The orange and yellow envelopes denote the 1- and
> 2-sigma{SE} regions.
> Douglass et al. use sigma{SE} to decide whether the multi-model
> mean
> trend is consistent with either of the observed trends. They
> conclude
> that the RSS and UAH trends lie outside of the yellow envelope
> (the
> 2-sigma{SE} region), and interpret this as evidence of a
> fundamental
> inconsistency between modeled and observed trends. As noted
> previously,
> Douglass et al. obtain this result because they fail to account
> for
> statistical uncertainty in the estimation of the RSS and UAH
> trends.
> They ignore the statistical error bars on the RSS and UAH trends
> (which
> are shown in Panel A). As is clear from Panel A, the statistical
> error
> bars on the RSS and UAH trends overlap with the Douglass et al.
> 2-sigma{SE} region. Had Douglass et al. accounted for statistical
> uncertainty in estimation of the observed trends, they would have
> been
> unable to conclude that all "UAH and RSS satellite trends are
> inconsistent with model trends".
> The second Figure plots values of our test statistic (d1) for the
> "paired trend test". The grey histogram is based on the values of
> d1 for
> the 49 tests involving the RSS T2LT trend and the simulated T2LT
> trends
> from 20c3m runs. The green histogram is for the 49 paired trend
> tests
> involving model 20c3m data and the UAH T2LT trend. Note that the
> d1
> distribution obtained with the UAH data is negatively skewed. This
> is
> because the numerator of the d1 test statistic is b{O} - b{M}, and
> the
> UAH tropical T2LT trend over 1979-1999 is smaller than most of the
> model
> trends (see Figure 1, panel A).
> The colored dots are values of the d1 test statistic for what I
> referred
> to previously as "TYPE2" tests. These tests are limited to the M
> models
> with multiple realizations of the 20c3m experiment. Here, M = 11.
> For
> each of these M models, I performed paired trend tests for all C
> unique
> combinations of trends pairs. For example, for a model with 5
> realizations of the 20c3m experiment, like GISS-EH, C = 10. The
> significance of trend differences is solely a function of "within-
> model"
> effects (i.e., is related to the different manifestations of
> natural
> internal variability superimposed on the underlying forced
> response).
> There are a total of 62 paired trend tests. Note that the
> separation of
> the colored symbols on the y-axis is for visual display purposes
> only,
> and facilitates the identification of results for individual models.
> The clear message from Figure 2 is that the values of d1 arising
> from
> internal variability alone are typically as large as the d1 values
> obtained by testing model trends against observational data. The
> two
> negative "outlier" values of d1 for the model-versus-observed
> trend
> tests involve the large positive trend in CCCma-CGCM3.1(T47). If
> you
> have keen eagle eyes, you'll note that the distribution of colored
> symbols is slightly skewed to the negative side. If you look at
> Panel A
> of Figure 1, you'll see that this skewness arises from the
> relatively
> small ensemble sizes. Consider results for the 5-member ensemble
> of
> 20c3m trends from the MRI-CGCM2.3.2. The trend in realization 1 is
> close
> to zero; trends in realizations 2, 3, 4, and 5 are large,
> positive, and
> vary between 0.27 to 0.37 degrees C/decade. So d1 is markedly
> negative
> for tests involving realization 1 versus realizations 2, 3, 4, and
> 5. If
> we showed non-unique combinations of trend pairs (e.g.,
> realization 2
> versus realization 1, as well as 1 versus 2), the distribution of
> colored symbols would be symmetric. But I was concerned that we
> might be
> accused of "double counting" if we did this....
> The third Figure is the most interesting one. You have not seen
> this
> yet. I decided to examine how the Douglass et al. "consistency
> test"
> behaves with synthetic data. I did this as a function of sample
> size N,
> for N values ranging from 19 (the number of models we used in the
> report) to 100. Consider the N = 19 case first. I generated 19
> synthetic
> time series using an AR-1 model of the form:
> xt(i) = a1 * (xt(i-1) - am) + zt(i) + am
> where a1 is the coefficient of the AR-1 model, zt(i) is a
> randomly-generated noise term, and am is a mean (set to zero
> here).
> Here, I set a1 to 0.86, close to the lag-1 autocorrelation of the
> T2LT anomaly data. The other free parameter is a scaling term
> which
> controls the amplitude of zt(i). I chose this scaling term to
> yield a
> temporal standard deviation of xt(i) that was close to the
> temporal
> standard deviation of the monthly-mean UAH T2LT anomaly data. The
> synthetic time series had the same length as the observational and
> model
> data (252 months), and monthly-mean anomalies were calculated in
> the
> same way as we did for observations and models.
> For each of these 19 synthetic time series, I first calculated
> least-squares linear trends and adjusted standard errors, and then
> performed the "paired trends". The test involves all 171 unique
> pairs of
> trends: b{1} versus b{2}, b{1} versus b{3},... b{1} versus b{19},
> b{2}
> versus b{3}, etc. I then calculate the rejection rates of the null
> hypothesis of "no significant difference in trend", for stipulated
> significance levels of 5%, 10%, and 20%. This procedure is
> repeated 1000
> times, with 1000 different realizations of 19 synthetic time
> series. We
> can therefore build up a distribution of rejection rates for N =
> 19, and
> then do the same for N = 20, etc.
> The "paired trend" results are plotted as the blue lines in Figure
> 3.
> Encouragingly, the percentage rejections of the null hypothesis
> are
> close to the theoretical expectations. The 5% significance tests
> yield a
> rejection rate of a little over 6%; 10% tests have a rejection
> rate of
> over 11%, and 20% tests have a rejection rate of 21%. I'm not
> quite sure
> why this slight positive bias arises. This bias does show some
> small
> sensitivity (1-2%) to choice of the a1 parameter and the scaling
> term.
> Different choices of these parameters can give rejection rates
> that are
> closer to the theoretical expectation. But my parameter choices
> for the
> AR-1 model were guided by the goal of generating synthetic data
> with
> roughly the same autocorrelation and variance properties as the
> data, and not by a desire to get as close as I possibly could to
> the
> theoretical rejection rates.
> So why is there a small positive bias in the empirically-
> determined
> rejection rates? Perhaps Francis can provide us with some guidance
> here.
> Karl believes that the answer may be partly linked to the skewness
> of
> the empirically-determined rejection rate distributions. For
> example,
> for the N = 19 case, and for 5% tests, values of rejection rates
> in the
> 1000-member distribution range from a minimum of 0 to a maximum of
> 24%,
> with a mean value of 6.7% and a median of 6.4%. Clearly, the
> minimum
> value is bounded by zero, but the maximum is not bounded, and in
> rare
> cases, rejection rates can be quite large, and influences the
> mean. This
> inherent skewness must make some contribution to the small
> positive bias
> in rejection rates in the "paired trends" test.
> What happens if we naively perform the paired trends test WITHOUT
> adjusting the standard errors of the trends for temporal
> autocorrelation
> effects? Results are shown by the black lines in Figure 3. If we
> ignore
> temporal autocorrelation, we get the wrong answer. Rejection rates
> for
> 5% tests are 60%!
> We did not publish results from any of these synthetic data
> experiments
> in our 2000 JGR paper. In retrospect, this is a bit of a shame,
> since
> Figure 3 nicely shows that the adjustment for temporal
> autocorrelation
> effects works reasonably well, while failure to adjust yields
> completely
> erroneous results.
> Now consider the red lines in Figure 3. These are the results of
> applying the Douglass et al. "consistency test" to synthetic data.
> Again, let's consider the N = 19 case first. I calculate the
> trends in
> all 19 synthetic time series. Let's consider the first of these 19
> time
> series as the surrogate observations. The trend in this time
> series,
> b{1}, is compared with the mean trend, b{Synth}, computed from the
> remaining 18 synthetic time series. The Douglass sigma{SE} is also
> computed from these 18 remaining trends. We then form a test
> statistic
> d2 = (b{1} - b{Synth}) / sigma{SE}, and calculate rejection rates
> for
> the null hypothesis of no significant difference between the mean
> trend
> and the trend in the surrogate observations. This procedure is
> then
> repeated with the trend in time series 2 as the surrogate
> observations,
> and b{Synth} and sigma{SE} calculated from time series 1, 3,
> 4,..19.
> This yields 19 different tests of the null hypothesis. Repeat
> 1,000
> times, and build up a distribution of rejection rates, as in the
> "paired
> trends" test.
> The results are truly alarming. Application of the Douglass et al.
> "consistency test" to synthetic data - data generated with the
> same
> underlying AR-1 model! - leads to rejection of the above-stated
> null
> hypothesis at least 65% of the time (for N = 19, 5% significance
> tests).
> As expected, rejection rates for the Douglass consistency test
> rise as
> N increases. For N = 100, rejection rates for 5% tests are nearly
> 85%.
> As my colleague Jim Boyle succinctly put it when he looked at
> these
> results, "This is a pretty hard test to pass".
> I think this nicely illustrates the problems with the statistical
> approach used by Douglass et al. If you want to demonstrate that
> modeled
> and observed temperature trends are fundamentally inconsistent,
> you
> devise a fundamentally flawed test is very difficult to pass.
> I hope to have a first draft of this stuff written up by the end
> of next
> week. If Leo is agreeable, Figure 4 of this GRL paper would show
> the
> vertical profiles of tropical temperature trends in the various
> versions
> of the RAOBCORE data, plus model results.
> Sorry to bore you with all the gory details. But as we've seen
> from
> Douglass et al., details matter.
> With best regards,
> Ben
> -------------------------------------------------------------------
> ---------
> Benjamin D. Santer
> Program for Climate Model Diagnosis and Intercomparison
> Lawrence Livermore National Laboratory
> P.O. Box 808, Mail Stop L-103
> Livermore, CA 94550, U.S.A.
> Tel: (925) 422-2486
> FAX: (925) 422-7675
> email:
> -------------------------------------------------------------------
> ---------

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