cc: "Thorne, Peter" <peter.thorneatXYZxyzoffice.gov.uk>, Tim Osborn <t.osbornatXYZxyz.ac.uk>

date: Fri Jan 11 15:42:44 2008

from: Phil Jones <p.jonesatXYZxyz.ac.uk>

subject: Re: [Fwd: Update on response to Douglass et al.]

to: Peter Stott <peter.stottatXYZxyzoffice.gov.uk>, santer1atXYZxyzl.gov

Peter,

We're working on this. Tim is in contact with Glenn McGregor who's

responding quite quickly despite being in Katmandu.

Ben is talking by phone to Tim at the moment!

See you in Boulder - I take it you'll still be able to come to IDAGs when you get your

new hat!

Cheers

Phil

At 15:36 11/01/2008, Peter Stott wrote:

Dear Ben,

I'm quite happy to stay out of it. I only got involved because I had had

a conversation with Paul Hardaker after the October Royal Met Soc

meeting where he was saying he was very keen for the Met Soc journals to

attract more submissions and it seemed to me that allowing a paper with

so many scientific flaws as the Douglass et al paper wasn't helping his

cause. It does though look like Paul and Ian Roulstone would be keen for

a response to be submitted to IJOC so maybe the board of IJOC could

expedite a speedy response ?

Best wishes for 2008 too !

Peter

On Fri, 2008-01-11 at 07:20 -0800, Ben Santer wrote:

> Dear Peter,

>

> MSU is like the "beast that will not die" in a bad B-grade horror movie.

> As Peter Thorne mentioned, I have been trying to lead an informal effort

> to craft a response to Douglass et al. As you'll be able to see from the

> forwarded email, we think that Douglass et al. had serious statistical

> flaws. My personal opinion is that publication of Douglass et al.

> reflects poorly on the IJoC and the Royal Met. Soc. It's unfortunate

> that folks like Singer and Christy are now trying to make political hay

> out of the IJoC's publication of Douglass et al. I think it would go

> some way towards setting the record straight if IJoC were willing to

> handle a response to Douglass et al. in an expeditious way. From my

> conversations with Phil Jones and Tim Osborn, it looks like IJoC might

> be prepared to do this.

>

> I'm hoping that our little "focus group" will be able to finalize a

> response by no later than the end of next week. If you are interested,

> I'd be very happy to add your name to our group's email list!

>

> Best regards, and best wishes for 2008,

>

> 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: santer1atXYZxyzl.gov

> ----------------------------------------------------------------------------

>

> email message attachment (Update on response to Douglass et al.)

> On Fri, 2008-01-11 at 07:20 -0800, Ben Santer wrote:

> > 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, 7337-7356]

> >

> > 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 RSS

> > 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 RSS

> > 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).

> >

> > REJECTION RATES FOR "PAIRED TREND TESTS, OBS-vs-MODEL

> > 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 CCSP

> > 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 UAH

> > 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 UAH

> > 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: santer1atXYZxyzl.gov

> > ----------------------------------------------------------------------------

> >

--

~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Dr. Peter Stott

Manager Understanding and Attributing Climate Change

Met Office Hadley Centre, Exeter, UK

Mail Address : Hadley Centre (Reading Unit)

Meteorology Building, University of Reading, Reading RG6 6BB

Tel: +44 (0)118 378 5613 Fax: +44 (0)118 378 5615

Mobile: 07753880683

E-mail:peter.stott@metoffice.gov.uk [1]http://www.metoffice.gov.uk

NOTE WILL ALSO BE AT EXETER PART OF EACH WEEK

~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Prof. Phil Jones

Climatic Research Unit Telephone +44 (0) 1603 592090

School of Environmental Sciences Fax +44 (0) 1603 507784

University of East Anglia

Norwich Email p.jonesatXYZxyz.ac.uk

NR4 7TJ

UK

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