## More on Hegerl et al 2006 Non-Confidence Intervals

There are a few other blogs that from time to time do detailed analyses of what people are doing, not dissimilar in format to what I do. Last year, in Apr 2006 shortly after publication, I observed here that the upper and lower confidence intervals of Hegerl et al crossed over.

In Feb 2007, Tapio Schneider published a Comment in Nature observing that the confidence intervals in Hegerl et al were wrong. Hegerl published a Reply and replaced the Supplementary Information with new data (I kept the old version in case anyone wants a comparison.) James Annan recently discussed the matter , linking to my graph, acknowledging it in a business-like way. About the new Supplementary Information, he said:

There is now a file giving the reconstruction back to 1500 with new confidence intervals, which no longer vanish or swap over. This new data doesn’t match the description of their method, or the results they plotted in their Fig 1 (which is almost surely a smoothed version of the original supplementary data).

He went on to say:

Hegerl et al used a regression to estimate past temperatures anomalies as a function of proxy data, and estimated the uncertainty in reconstructed temperature as being entirely due to the uncertainty in the regression coefficient. The problem with this manifests itself most clearly when the tree ring anomaly is zero, as in this event the uncertainty in the reconstructed temperature is also zero!

Maybe UC (or Jean S who we haven’t heard from for a while) can comment on this. This comment still doesn’t seem right to me as I can’t think of why the uncertainty would be zero merely because all of the uncertainty was allocated to the regression coefficient. I still can’t get a foothold on what they’re doing here; Annan said that Tapio Schneider had been unsuccessful in getting Hegerl to document what they did in any of the calculations. I’ll write but I’m not optimistic about my chances. I’m up to about 20 emails with Crowley trying to find out how they got their Mongolia and Urals series, without any success.

Eli Rabett observed that Huang et al appeared to have done the same thing in a borehole study. In the caption, Huang refer to Bayesian methods being used, so maybe there’s a clue for someone. Whatever these folks are doing, it’s not a totally isolated incident. Who knows – one day,we might even find out how the MBH99 confidence intervals were calculated – presently one of the 21st Century Hilbert Problems in climate science.

References:
Hegerl JClim 2006 here
Hegerl Nature 2006 here
Hegerl SI here

1. John Hekman
Posted May 4, 2007 at 11:32 AM | Permalink

if y = a + bx + e, and you want to know the variance of the estimated value, y^, that variance is not zero when you are comparing the actual time series with the fitted values and one of the fitted values is equal to the actual value. If that is what he is saying here, he’s nuts.

You just have to look at the ANOVA. http://en.wikipedia.org/wiki/ANOVA

2. Posted May 4, 2007 at 4:18 PM | Permalink

Confidence intervals, regardless of method, cannot vanish or cross over. If one does end up with such confidence intervals, it is a sure sign that something is seriously wrong in the way calculations have been done. If it happened to me, I would withdraw to an isolated room, not get out until I figured out my error and I would be ashamed to tell anyone about whatever stupid mistake I made.

However, this paper got published. Sad.

Here is what I mean: The width of the confidence interval for mean response in a simple OLS regression with one independent variable depends on the standard error of the mean response (which, in turn, depends on the x-value at which mean response is being evaluated). We have, from the Intro Stats textbook I use in the undergrad stats class I teach,

$\mathrm{SE}_{\hat{\mu}} = s\sqrt{\frac{1}{n} + \frac{(x^*-\bar{x})^2}{\Sum (x_i-\bar{x})^2}}$

If $x^* = \bar{x}$, this reduces to $s\sqrt{\frac{1}{n}}$ which cannot be zero (unless the regression line is a perfect fit) because s is the square root of MSE.

Now, confidence intervals for mean response will be narrower than prediction confidence intervals (for the same confidence) but they cannot vanish and the lower and upper bounds cannot cross.

I am baffled.

Sinan

3. 2dogs
Posted May 4, 2007 at 4:21 PM | Permalink

It looks like the uncertainty is all assigned to the regression co-effecient of the anomoly (i.e. to b in y = bx + e); consequently, the upper and lower bounds flip over when the anomoly passes zero.

4. Posted May 4, 2007 at 4:22 PM | Permalink

Correction to #2:

In the formula for the standard error of mean response, there is a sum $\Sigma$ sign missing from the denominator of the second term in the square root.

Also, I mention the undergrad intro stats textbook to underline the fact that this is basic, elementary stuff. Vanishing confidence intervals or crossing upper and lower bounds is an indication that the author of the article ought not be trusted to balance his own checkbook.

Sinan

5. Steve McIntyre
Posted May 4, 2007 at 10:07 PM | Permalink

I sent the following inquiry to Gabi Hegerl:

I have not received the requested information on the Mongolian and Urals series from Tom. I realize that you have other concerns but this has been going on far too long.

Also can you provide a replicable description of how you calculated your confidence intervals. I realize that the original SI required correction, but in the wake of this there is no formal description of your procedures or statistical references. If it would save you time to merely provide source code for the results, that would be fine with me.

6. Steve McIntyre
Posted May 5, 2007 at 7:46 AM | Permalink

#5. Gabi Hegerl replied as follows:

Steve, Tom produced the individual timeseries, but not with fortran code but with other software, so I am not sure there is a source code.

The correction in the SI was minimal and it would have been totally sufficient to change order 3 words in the caption, but I thought it was more helpful to instead link the reconstructions with full uncertainty] range. The description in the SI is very complete on that, particularly together with my J Climate paper. It should make it completely reproducable.

Gabi

7. Nicholas
Posted May 5, 2007 at 8:42 AM | Permalink

Did you plot that diagram yourself? If so, is the R code easily available somewhere?

I’m asking because they look an awful lot like they are merely scaled versions of each other. It would be interesting to check if that’s true.

8. Steve McIntyre
Posted May 5, 2007 at 9:12 AM | Permalink

I’ll try to post up the code today. It might be an interesting project for statistically-interested people to decode their uncertainty methodology. I’ll post up as much relevant data as I have.

9. Henry
Posted May 5, 2007 at 5:45 PM | Permalink

It looks to me as if they originally used a statistical recipe in the wrong context.

Trying to imagine a proper context: suppose you tried to regress national GDP against national population using data for 100 countries. $y_i=\alpha +\beta x_i +\varepsilon_i$ would be a bad model since it is obvious that a country with a tiny population would have a tiny GDP. $y_i=\beta x_i +\varepsilon_i$ would be almost as bad as the absolute values of errors would clearly be related to population. $y_i=\beta \varepsilon_i x_i$ starts to make more sense.

But that model only makes sense if all the values are positive and if errors tend to increase with the independent variable. That doesn’t apply here, so it was the wrong method to apply. It probably stemmed from a desire to have everything at zero in the base period for calculating anomalies. And the graph should have been spotted by the peer reviewers.

10. Vince Causey
Posted May 6, 2007 at 12:06 PM | Permalink

I have heard it said before, that a lot of these results that involve statistical techniques lack the input of suitably qualified statisticians. Am I right in thinking that elementary statistical errors are being made due to lack of competence? If this is the case, then the quality of a lot of this kind of research must be suspect.

11. Posted May 6, 2007 at 1:04 PM | Permalink

Very briefly:

something odd in the manuscript figure 2 as well, cross overs..

BTW,

‘negative bias of the variance of the reconstruction’ in supplementary refers to vS04. I believe that this negative bias is a result of ‘natural calibration’ assumption, i.e. optimal solution in the case where P and T are obtained from joint normal distribution. I’ll return to this topic later ( and if I’m wrong I just disappear ;) )

Confidence and Conflict in Multivariate Calibration (PJ Brown, R Sundberg, Journal of the Royal Statistical Society, Ser B, Vol 49, No 1, 1987)

Those papers contain some ideas how to deal with uncertainties in this context (filtering theory is another way, but it doesn’t seem to interest climate people ).

12. Tim
Posted May 8, 2007 at 7:22 PM | Permalink

Here is how one can get “confidence” intervals of zero width in temperature reconstructions:

1) Estimate a regression model

T – [T] = b(p – [p] + eta) + eps (*)

where T-[T] are temperature anomalies (mean temperature [T]), p-[p] are proxy anomalies, and eta and eps are error terms.

2) “Reconstruct” temperature anomalies by taking expected values in the regression model (*) and plugging in estimated regression coefficients b’ (and estimated mean values [T] and [p]).
-> The “reconstructed” temperature anomalies T-[T] are zero for any value b’ of the estimated regression coefficient if the proxy anomaly p-[p] is zero.

3) Vary the estimated regression coefficient b’ within estimated confidence limits and “reconstruct” temperature anomalies as in (2) for each value of b’.
-> The “reconstructed” temperature anomalies will still be zero for all values of b’ whenever p-[p] is zero.

4) If one infers confidence intervals from the reconstructed temperature anomalies for the different b’ for each year, they will have zero width whenever p-[p] is zero. Of course, it makes no sense to estimate confidence intervals in this way.

This seems to be what Hegerl et al. were doing and what led to their manifestly wrong confidence intervals for the reconstructed temperatures.

Schneider’s point in the Nature comment, however, seems to be more general. Hegerl et al. base their inference about climate sensitivity on the residual difference between the “reconstructed” temperature anomalies and temperature anomalies simulated with an EBM. Schneider points out that

What should enter the calculation of the
likelihoods of the temperature-anomaly time
series T-[T] is the estimated variance of the
residuals r, not just the sample variance
proportional to their sum of squares, sum(r^2).

While the error terms eta and eps do not enter the expected value of the difference between EBM temperature anomalies and reconstructed temperature anomalies, they do enter the variance of the residual difference. The variance of the estimated regression coefficients contributes to the residual variance, but so do the variances of eta and eps. This is elementary regression analysis: The variances of eta and eps are generally greater (by a factor of order sample size) than the variance of b’.

13. Posted May 9, 2007 at 6:59 AM | Permalink

#12

Clarifying posts are appreciated, thks (and posters should not be worried about making mistakes, if you make an explicit mistake, gavin drops by and corrects it, so no worries ). It is 1959 in climate science in statistics sense, Williams just published Regression Analysis. Next year will be interesting, as Kalman will publish his A New Approach to Linear Filtering and Prediction Problems.

14. Steve McIntyre
Posted May 9, 2007 at 7:06 AM | Permalink

#12. That makes total sense as an explanation. That’s unbelievable. What a joke. I’ll make a separate post on it in a few days.

15. bender
Posted May 15, 2007 at 10:56 PM | Permalink

It’s hard to imagine an error of this magnitude being made by an author and then not being caught by co-authors, internal reviewers, peer reviewers, co-editors, editor. The crossing over of the curves is an obvious sign something’s gone wrong. An undergraduate could tell you that.

16. bender
Posted May 15, 2007 at 11:11 PM | Permalink

Steve M, look at the original confidence interval in the Nature 2006 paper, the region in gray. Why is the confidence interval so thick in those problem areas where the upper and lower bounds cross over? The answer, which you get in the form of a delay in graphics redrawing when you zoom in close, is that the authors have heavily thickened the lines of the gray graphic object. (If they were thin, the pinch would be obvious.) Now why would they do that? To hide the fact that the confidence region pinches as the bounds cross over?

Anyways, this is probably why reviewers never caught the error. But it would be nice to know to what degree this deception was intentional.

• bender
Posted Jul 9, 2010 at 9:03 AM | Permalink

“Hide the crossover”.

17. bender
Posted May 15, 2007 at 11:39 PM | Permalink

The new SI at least answers john lichtenstein’s #5 from the previous thread:

Am I the only one perplexed with the confidence interval around 1400, 1650, and 1750?

The new SI (which starts from 1505) shows the CI’s around 1650 and 1750 to be very wide.

Still, as Annan argues, the CI’s are wrong. In order to get the uncertainty on the inferred value, the uncertainty in the observed value (the proxy value on which the temp reconstruction is based) has to propagate through the uncertainty in the regression coefficients. It makes no sense to assume all the uncertainty comes from the standard errors in the estimated regression coefficients. Some of it must come from sampling error from the estimation of the means.

It is very important to know exactly what these folks are doing.

18. Posted May 16, 2007 at 1:46 AM | Permalink

Some notes / questions:

TLS uses first principal component, minimizes perpendicular distances from data points to the line ( a new line to my calibration-line-plot ) ?

In Hegerl J. Climate paper

Note that if the uncertainties in the paleo reconstruction are much larger than in instrumental data, an alternative is the use of inverse regression, neglecting error in instrumental data (Coehlo et al., 2004).

I think this is an misunderstanding. IMO Coehlo explains CCE and ICE quite well, and Hegerl et al didn’t read carefully. ICE requires prior distribution for temperatures, and another viewpoint of ICE was just developed in http://www.climateaudit.org/?p=1515#comment-108922 and following comments. If I were a reviewer, I’d stop reading that manuscript right there, page 7. ( I don’t have the final version, was anything corrected? ). I’m not surprised that their CIs went wrong..

19. bender
Posted May 16, 2007 at 7:41 AM | Permalink

Suppose:
inferred Temperature = A * Proxy measure + B

where A, B are regression parameters, each with standard errors, and Proxy P is subject to sampling error.
Then the error in the inference T is the quadrature sum of the errors in A*P and B, and the error in A*P here is the straight
sum of the relative errors in A and P.

Is that not the correct way to compute the confidence level for a quantity inferred from an error-prone calibration? That’s what I learned in high school physics, anyways.

20. Steve McIntyre
Posted May 16, 2007 at 7:48 AM | Permalink

Gabi Hegerl has sent me the following email last week in response to my request for further particulars on her method:

if you tell me which part you find hard to understand, I can send you an algorithm. The records are processed by a number of programs. Tom;s teaching is over for the semester so I think you’ll get more detail out of him soon.

Just so that I meet the requirements of other readers, UC and bender, can you summarize any questions? BTW I got a copy of the Hegerl J CLim article as published posted up here Ther references ot an SI have been removed and there is no SI at the J Climate website.

21. Earle Williams
Posted May 16, 2007 at 1:43 PM | Permalink

Re #20

Steve M,

The URL for the Hegerl paper is a bit off. It looks to be http://data.climateaudit.org/pdf/Hegerll07.jclim.pdf

22. Steve McIntyre
Posted May 21, 2007 at 10:17 PM | Permalink

James Annan writes:

Zero-width confidence intervals are not necessarily wrong. They are rather unconventional, perhaps, but that doesn’t make them incorrect.

23. Willis Eschenbach
Posted May 22, 2007 at 2:55 PM | Permalink

Zero-width confidence intervals are not necessarily wrong. They are rather unconventional, perhaps, but that doesn’t make them incorrect.

Man, that’s just plain and fancy footwork. I can’t offhand think of any physical measurement that has a confidence interval of zero. Examples, anyone?

w.

24. bender
Posted May 22, 2007 at 3:10 PM | Permalink

Re #23 That remark baffled me, too. (I didn’t say anything because I’ve been commenting too much lately.)