The insularity critique of climate science

by VipulNaik 5y9th Jul 201418 min read40 comments

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Note: Please see this post of mine for more on the project, my sources, and potential sources for bias.

One of the categories of critique that have been leveled against climate science is the critique of insularity. Broadly, it is claimed that the type of work that climate scientists are trying to do draws upon insight and expertise in many other domains, but climate scientists have historically failed to consult experts in those domains or even to follow well-documented best practices.

Some takeaways/conclusions

Note: I wrote a preliminary version of this before drafting the post, but after having done most of the relevant investigation. I reviewed and edited it prior to publication. Note also that I don't justify these takeaways explicitly in my later discussion, because a lot of these come from general intuitions of mine and it's hard to articulate how the information I received explicitly affected my reaching the takeaways. I might discuss the rationales behind these takeaways more in a later post.

  • Many of the criticisms are broadly on the mark: climate scientists should have consulted best practices in other domains, and in general should have either followed them or clearly explained the reasons for divergence.
  • However, this criticism is not unique to climate science: academia in general has suffered from problems of disciplines being relatively insular (UPDATE: Here's Robin Hanson saying something similar). And many similar things may be true, albeit in different ways, outside academia.
  • One interesting possibility is that bad practices here operate via founder effects: for an area that starts off as relatively obscure and unimportant, setting up good practices may not be considered important. But as the area grows in importance, it is quite rare for the area to be cleaned up. People and institutions get used to the old ways of doing things. They have too much at stake to make reforms. This does suggest that it's important to get things right early on.
  • (This is speculative, and not discussed in the post): The extent of insularity of a discipline seems to be an area where a few researchers can have significant effect on the discipline. If a few reasonably influential climate scientists had pushed for more integration with and understanding of ideas from other disciplines, the history of climate science research would have been different.

Relevant domains they may have failed to use or learn from

  1. Forecasting research: Although climate scientists were engaging in an exercise that had a lot to do with forecasting, they neither cited research nor consulted experts in the domain of forecasting.
  2. Statistics: Climate scientists used plenty of statistics in their analysis. They did follow the basic principles of statistics, but in many cases used them incorrectly or combined them with novel approaches that were nonstandard and did not have clear statistical literature justifying the use of such approaches.
  3. Programming and software engineering: Climate scientists used a lot of code both for their climate models and for their analyses of historical climate. But their code failed basic principles of decent programming, let alone good software engineering principles such as documentation, unit testing, consistent variable names, and version control.
  4. Publication of data, metadata, and code: This is a phenomenon becoming increasingly common in some other sectors of academia and industry. Climate scientists they failed to learn from econometrics and biomedical research, fields that had been struggling with some qualitatively similar problems and that had been moving to publishing data, metadata, and code.

Let's look at each of these critiques in turn.

Critique #1: Failure to consider forecasting research

We'll devote more attention to this critique, because it has been made, and addressed, cogently in considerable detail.

J. Scott Armstrong (faculty page, Wikipedia) is one of the big names in forecasting. In 2007, Armstrong and Kesten C. Green co-authored a global warming audit (PDF of paper, webpage with supporting materials) for the Forecasting Principles website. that was critical of the forecasting exercises by climate scientists used in the IPCC reports.

Armstrong and Green began their critique by noting the following:

  • The climate science literature did not reference any of the forecasting literature, and there was no indication that they had consulted forecasting experts, even though what they were doing was to quite an extent a forecasting exercise.
  • There was only one paper, by Stewart and Glantz, dating back to 1985, that could be described as a forecasting audit, and that paper was critical of the methodology of climate forecasting. And that paper appears to have been cited very little in the coming years.
  • Armstrong and Green tried to contact leading climate scientists. Of the few who responded, none listed specific forecasting principles they followed, or reasons for not following general forecasting principles. They pointed to the IPCC reports as the best source for forecasts. Armstrong and Green estimated that the IPCC report violated 72 of 89 forecasting principles they were able to rate (their list of forecasting principles includes 140 principles, but they judged only 127 as applicable to climate forecasting, and were able to rate only 89 of them). No climate scientists responded to their invitation to provide their own ratings for the forecasting principles.

How significant are these general criticisms? It depends on the answers to the following questions:

  • In general, how much credence do you assign to the research on forecasting principles, and how strong a prior do you have in favor of these principles being applicable to a specific domain? I think the answer is that forecasting principles as identified on the Forecasting Principles website are a reasonable starting point, and therefore, any major forecasting exercise (or exercise that implicitly generates forecasts) should at any rate justify major points of departure from these principles.
  • How representative are the views of Armstrong and Green in the forecasting community? I have no idea about the representativeness of their specific views, but Armstrong in particular is high-status in the forecasting community (that I described a while back) and the Forecasting Principles website is one of the go-to sources, so material on the website is probably not too far from views in the forecasting community. (Note: I asked the question on Quora a while back, but haven't received any answers).

So it seems like there was arguably a failure of proper procedure in the climate science community in terms of consulting and applying practices from relevant domains. Still, how germane was it to the quality of their conclusions? Maybe it didn't matter after all?

In Chapter 12 of The Signal and the Noise, statistician and forecaster Nate Silver offers the following summary of Armstrong and Green's views:

  • First, Armstrong and Green contend that agreement among forecasters is not related to accuracy—and may reflect bias as much as anything else. “You don’t vote,” Armstrong told me. “That’s not the way science progresses.”
  • Next, they say the complexity of the global warming problem makes forecasting a fool’s errand. “There’s been no case in history where we’ve had a complex thing with lots of variables and lots of uncertainty, where people have been able to make econometric models or any complex models work,” Armstrong told me. “The more complex you make the model the worse the forecast gets.”
  • Finally, Armstrong and Green write that the forecasts do not adequately account for the uncertainty intrinsic to the global warming problem. In other words, they are potentially overconfident.


Silver, Nate (2012-09-27). The Signal and the Noise: Why So Many Predictions Fail-but Some Don't (p. 382). Penguin Group US. Kindle Edition.

Silver addresses each of these in his book (read it to know what he says). Here are my own thoughts on the three points as put forth by Silver:

  • I think consensus among experts (to the extent that it does exist) should be taken as a positive signal, even if the experts aren't good at forecasting. But certainly, the lack of interest or success in forecasting should dampen the magnitude of the positive signal. We should consider it likely that climate scientists have identified important potential phenomena, but should be skeptical of any actual forecasts derived from their work.
  • I disagree somewhat with this point. I think forecasting could still be possible, but as of now, there is little of a successful track record of forecasting (as Green notes in a later draft paper). So forecasting efforts, including simple ones (such as persistence, linear regression, random walk with drift) and ones based on climate models (both the ones in common use right now and others that give more weight to the PDO/AMO), should continue but the jury is still out on the extent to which they work.
  • I agree here that many forecasters are potentially overconfident.

Some counterpoints to the Armstrong and Green critique:

  • One can argue that what climate scientists are doing isn't forecasting at all, but scenario analysis. After all, the IPCC generates scenarios, but not forecasts. But as I discussed in an earlier post, scenario planning and forecasting are closely related, and even if scenarios aren't direct explicit unconditional forecasts, they often involve implicit conditional forecasts. To its credit, the IPCC does seem to have used some best practices from the scenario planning literature in generating its emissions scenarios. But that is not part of the climate modeling exercise of the IPCC.
  • Many other domains that involve planning for the future don't reference the forecasting literature. Examples include scenario planning (discussed here) and the related field of futures studies (discussed here). Insularity of disciplines from each other is a common feature (or bug) in much of academia. Can we really expect or demand that climate scientists hold themselves to a higher standard?

UPDATE: I forgot to mention in my original draft of the post that Armstrong challenged Al Gore to a bet pitting Armstrong's No Change model with the IPCC model. Gore did not accept the bet, but Armstrong created the website (here) anyway to record the relative performance of the two models.

UPDATE 2: Read drnickbone's comment and my replies for more information on the debate. drnickbone in particular points to responses from Real Climate and Skeptical Science, that I discuss in my response to his comment.

Critique #2: Inappropriate or misguided use of statistics, and failure to consult statisticians

To some extent, this overlaps with Critique #1, because best practices in forecasting include good use of statistical methods. However, the critique is a little broader. There are many parts of climate science not directly involved with forecasting, but where statistical methods still matter. Historical climate reconstruction is one such example. The purpose of these is to get a better understanding of the sorts of climate that could occur and have occurred, and how different aspects of the climate correlated. Unfortunately, historical climate data is not very reliable. How do we deal with different proxies for the climate variables we are interested in so that we can reconstruct them? A careful use of statistics is important here.

Let's consider an example that's quite far removed from climate forecasting, but has (perhaps undeservedly) played an important role in the public debate on global warming: Michael Mann's famed hockey stick (Wikipedia), discussed in detail in Mann, Bradley and Hughes (henceforth, MBH98) (available online here). The major critiques of the paper arose in a series of papers by McIntyre and McKitrick, the most important of them being their 2005 paper in Geophysical Research Letters (henceforth, MM05) (available online here).

I read about the controversy in the book The Hockey Stick Illusion by Andrew Montford (Amazon, Wikipedia), but the author also has a shorter article titled Caspar and the Jesus paper that covers the story as it unfolds from his perspective. While there's a lot more to the hockey stick controversy than statistics alone, some of the main issues are statistical.

Unfortunately, I wasn't able to resolve the statistical issues myself well enough to have an informed view. But my very crude intuition, as well as the statements made by statisticians as recorded below, supports Montford's broad outline of the story. I'll try to describe the broad critiques leveled from the statistical perspective:

  • Choice of centering and standardization: The data was centered around the 20th century, a method known as short-centering, and bound to create a bias in favor of picking hockey stick-like shapes when doing principal components analysis. Each series was also standardized (divided by the standard deviation for the 20th century), which McIntyre argued was inappropriate.
  • Unusual choice of statistic used for significance: MBH98 used a statistic called the RE statistic (reduction of error statistic). This is a fairly unusual statistic to use. In fact, it doesn't have a Wikipedia page, and practically the only stuff on the web (on Google and Google Scholar) about it was in relation to tree-ring research (the proxies used in MBH98 were tree rings). This should seem suspicious: why is tree-ring research using a statistic that's basically unused outside the field? There are good reasons to avoid using statistical constructs on which there is little statistical literature, because people don't have a feel for how they work. MBH98 could have used the R^2 statistic instead, and in fact, they mentioned it in their paper but then ended up not using it.
  • Incorrect calculation of significance threshold: MM05 (plus subsequent comments by McIntyre) claims that not only is the RE statistic nonstandard, there were problems with the way MBH98 used it. First off, there is no theoretical distribution of the RE statistic, so calculating the cutoff needed to attain a particular significance level is a tricky exercise (this is one of many reasons why using a RE statistic may be ill-advised, according to McIntyre). MBH98 calculated the cutoff value for 99% significance incorrectly to be 0. The correct value according to McIntyre was about 0.54, whereas the actual RE statistic value for the data set in MBH98 was 0.48, i.e., not close enough. A later paper by Ammann and Wahl, cited by many as a vindication of MBH98, computed a similar cutoff of 0.52, so that the actual RE statistic value failed the significance test. So how did it manage to vindicate MBH98 when the value of the RE statistic failed the cutoff? They appear to have employed a novel statistical procedure, coming up with something called a calibration/verification RE ratio. McIntyre was quite critical of this, for reasons he described in detail here.

There has been a lengthy debate on the subject, plus two external inquiries and reports on the debate: the NAS Panel Report headed by Gerry North, and the Wegman Report headed by Edward Wegman. Both of them agreed with the statistical criticisms made by McIntyre, but the NAS report did not make any broader comments on what this says about the discipline or the general hockey stick hypothesis, while the Wegman report made more explicit criticism.

The Wegman Report made the insularity critique in some detail:

In general, we found MBH98 and MBH99 to be somewhat obscure and incomplete and the criticisms of MM03/05a/05b to be valid and compelling. We also comment that they were attempting to draw attention to the discrepancies in MBH98 and MBH99, and not to do paleoclimatic temperature reconstruction. Normally, one would try to select a calibration dataset that is representative of the entire dataset. The 1902-1995 data is not fully appropriate for calibration and leads to a misuse in principal component analysis. However, the reasons for setting 1902-1995 as the calibration point presented in the
narrative of MBH98 sounds reasonable, and the error may be easily overlooked by someone not trained in statistical methodology. We note that there is no evidence that Dr. Mann or any of the other authors in paleoclimatology studies have had significant interactions with mainstream statisticians.

In our further exploration of the social network of authorships in temperature reconstruction, we found that at least 43 authors have direct ties to Dr. Mann by virtue of coauthored papers with him. Our findings from this analysis suggest that authors in the area of paleoclimate studies are closely connected and thus ‘independent studies’ may not be as independent as they might appear on the surface. This committee does not believe that web logs are an appropriate forum for the scientific debate on this issue.

It is important to note the isolation of the paleoclimate community; even though they rely heavily on statistical methods they do not seem to be interacting with the statistical community. Additionally, we judge that the sharing of research materials, data and results was haphazardly and grudgingly done. In this case we judge that there was too much reliance on peer review, which was not necessarily independent. Moreover, the work has been sufficiently politicized that this community can hardly reassess their public positions without losing credibility. Overall, our committee believes that Mann’s assessments that the decade of the 1990s was the hottest decade of the millennium and that 1998 was the hottest year of the millennium cannot be supported by his analysis.

McIntyre has a lengthy blog post summarizing what he sees as the main parts of the NAS Panel Report, the Wegman Report, and other statements made by statisticians critical of MBH98.

Critique #3: Inadequate use of software engineering, project management, and coding documentation and testing principles

In the aftermath of Climategate, most public attention was drawn to the content of the emails. But apart from the emails, data and code was also leaked, and this gave the world an inside view of the code that's used to simulate the climate. A number of criticisms of the coding practice emerged.

Chicago Boyz had a lengthy post titled Scientists are not Software Engineers that noted the sloppiness in the code, and some of the implications, but was also quick to point out that poor-quality code is not unique to climate science and is a general problem with large-scale projects that arise from small-scale academic research growing beyond what the coders originally intended, but with no systematic efforts being made to refactor the code (if you have thoughts on the general prevalence of good software engineering practices in code for academic research, feel free to share them by answering my Quora question here, and if you have insights on climate science code in particular, answer my Quora question here). Below are some excerpts from the post:

No, the real shocking revelation lies in the computer code and data that were dumped along with the emails. Arguably, these are the most important computer programs in the world. These programs generate the data that is used to create the climate models which purport to show an inevitable catastrophic warming caused by human activity. It is on the basis of these programs that we are supposed to massively reengineer the entire planetary economy and technology base.

The dumped files revealed that those critical programs are complete and utter train wrecks.

[...]

The design, production and maintenance of large pieces of software require project management skills greater than those required for large material construction projects. Computer programs are the most complicated pieces of technology ever created. By several orders of magnitude they have more “parts” and more interactions between those parts than any other technology.

Software engineers and software project managers have created procedures for managing that complexity. It begins with seemingly trivial things like style guides that regulate what names programmers can give to attributes of software and the associated datafiles. Then you have version control in which every change to the software is recorded in a database. Programmers have to document absolutely everything they do. Before they write code, there is extensive planning by many people. After the code is written comes the dreaded code review in which other programmers and managers go over the code line by line and look for faults. After the code reaches its semi-complete form, it is handed over to Quality Assurance which is staffed by drooling, befanged, malicious sociopaths who live for nothing more than to take a programmer’s greatest, most elegant code and rip it apart and possibly sexually violate it. (Yes, I’m still bitter.)

Institutions pay for all this oversight and double-checking and programmers tolerate it because it is impossible to create a large, reliable and accurate piece of software without such procedures firmly in place. Software is just too complex to wing it.

Clearly, nothing like these established procedures was used at CRU. Indeed, the code seems to have been written overwhelmingly by just two people (one at a time) over the past 30 years. Neither of these individuals was a formally trained programmer and there appears to have been no project planning or even formal documentation. Indeed, the comments of the second programmer, the hapless “Harry”, as he struggled to understand the work of his predecessor are now being read as a kind of programmer’s Icelandic saga describing a death march through an inexplicable maze of ineptitude and boobytraps.

[...]

A lot of the CRU code is clearly composed of hacks. Hacks are informal, off-the-cuff solutions that programmers think up on the spur of the moment to fix some little problem. Sometimes they are so elegant as to be awe inspiring and they enter programming lore. More often, however, they are crude, sloppy and dangerously unreliable. Programmers usually use hacks as a temporary quick solution to a bottleneck problem. The intention is always to come back later and replace the hack with a more well-thought-out and reliable solution, but with no formal project management and time constraints it’s easy to forget to do so. After a time, more code evolves that depends on the existence of the hack, so replacing it becomes a much bigger task than just replacing the initial hack would have been.

(One hack in the CRU software will no doubt become famous. The programmer needed to calculate the distance and overlapping effect between weather monitoring stations. The non-hack way to do so would be to break out the trigonometry and write a planned piece of code to calculate the spatial relationships. Instead, the CRU programmer noticed that that the visualization software that displayed the program’s results already plotted the station’s locations so he sampled individual pixels on the screen and used the color of the pixels between the stations to determine their location and overlap! This is a fragile hack because if the visualization changes the colors it uses, the components that depend on the hack will fail silently.)

For some choice comments excerpted from a code file, see here.

Critique #4: Practices of publication of data, metadata, and code (that had gained traction in other disciplines)

When McIntyre wanted to replicate MBH98, he emailed Mann asking for his data and code. Mann, though initially cooperative, soon started trying to fed McIntyre off. Part of this was because he thought McIntyre was out to find something wrong with his work (a well-grounded suspicion). But part of it was also that his data and code were a mess. He didn't maintain them in a way that he'd be comfortable sharing them around to anybody other than an already sympathetic academic. And, more importantly, as Mann's colleague Stephen Schneider noted, nobody asked for the code and underlying data during peer review. And most journals at the time did not require authors to submit or archive their code and data at the time of submission or acceptance of their paper. This also closely relates to Critique #3: a requirement or expectation that one's data and code would be published along with one's paper might make people more careful to follow good coding practices and avoid using various "tricks" and "hacks" in their code.

Here's how Andrew Montford puts it in The Hockey Stick Illusion:

The Hockey Stick affair is not the first scandal in which important scientific papers underpinning government policy positions have been found to be non-replicable – McCullough and McKitrick review a litany of sorry cases from several different fields – but it does underline the need for a more solid basis on which political decision-making should be based. That basis is replication. Centuries of scientific endeavour have shown that truth emerges only from repeated experimentation and falsification of theories, a process that only begins after publication and can continue for months or years or decades thereafter. Only through actually reproducing the findings of a scientific paper can other researchers be certain that those findings are correct. In the early history of European science, publication of scientific findings in a journal was usually adequate to allow other researchers to replicate them. However, as science has advanced, the techniques used have become steadily more complicated and consequently more difficult to explain. The advent of computers has allowed scientists to add further layers of complexity to their work and to handle much larger datasets, to the extent that a journal article can now, in most cases, no longer be considered a definitive record of a scientific result. There is simply insufficient space in the pages of a print journal to explain what exactly has been done. This has produced a rather profound change in the purpose of a scientific paper. As geophysicist Jon Claerbout puts it, in a world where powerful computers and vast datasets dominate scientific research, the paper ‘is not the scholarship itself, it is merely advertising of the scholarship’.b The actual scholarship is the data and code used to generate the figures presented in the paper and which underpin its claims to uniqueness. In passing we should note the implications of Claerbout’s observations for the assessment for our conclusions in the last section: by using only peer review to assess the climate science literature, the policymaking community is implicitly expecting that a read-through of a partial account of the research performed will be sufficient to identify any errors or other problems with the paper. This is simply not credible. With a full explanation of methodology now often not possible from the text of a paper, replication can usually only be performed if the data and code are available. This is a major change from a hundred years ago, but in the twenty-first century it should be a trivial problem to address. In some specialisms it is just that. We have seen, however, how almost every attempt to obtain data from climatologists is met by a wall of evasion and obfuscation, with journals and funding bodies either unable or unwilling to assist. This is, of course, unethical and unacceptable, particularly for publicly funded scientists. The public has paid for nearly all of this data to be collated and has a right to see it distributed and reused. As the treatment of the Loehle paper shows,c for scientists to open themselves up to criticism by allowing open review and full data access is a profoundly uncomfortable process, but the public is not paying scientists to have comfortable lives; they are paying for rapid advances in science. If data is available, doubts over exactly where the researcher has started from fall away. If computer code is made public too, then the task of replication becomes simpler still and all doubts about the methodology are removed. The debate moves on from foolish and long-winded arguments about what was done (we still have no idea exactly how Mann calculated his confidence intervals) onto the real scientific meat of whether what was done was correct. As we look back over McIntyre’s work on the Hockey Stick, we see that much of his time was wasted on trying to uncover from the obscure wording of Mann’s papers exactly what procedures had been used. Again, we can only state that this is entirely unacceptable for publicly funded science and is unforgiveable in an area of such enormous policy importance. As well as helping scientists to find errors more quickly, replication has other benefits that are not insignificant. David Goodstein of the California Insitute of Technology has commented that the possibility that someone will try to replicate a piece of work is a powerful disincentive to cheating – in other words, it can help to prevent scientific fraud.251 Goodstein also notes that, in reality, very few scientific papers are ever subject to an attempt to replicate them. It is clear from Stephen Schneider’s surprise when asked to obtain the data behind one of Mann’s papers that this criticism extends into the field of climatology.d In a world where pressure from funding agencies and the demands of university careers mean that academics have to publish or perish, precious few resources are free to replicate the work of others. In years gone by, some of the time of PhD students might have been devoted to replicating the work of rival labs, but few students would accept such a menial task in the modern world: they have their own publication records to worry about. It is unforgiveable, therefore, that in paleoclimate circles, the few attempts that have been made at replication have been blocked by all of the parties in a position to do something about it. Medical science is far ahead of the physical sciences in the area of replication. Doug Altman, of Cancer Research UK’s Medical Statistics group, has commented that archiving of data should be mandatory and that a failure to retain data should be treated as research misconduct.252 The introduction of this kind of regime to climatology could have nothing but a salutary effect on its rather tarnished reputation. Other subject areas, however, have found simpler and less confrontational ways to deal with the problem. In areas such as econometrics, which have long suffered from politicisation and fraud, several journals have adopted clear and rigorous policies on archiving of data. At publications such as the American Economic Review, Econometrica and the Journal of Money, Credit and Banking, a manuscript that is submitted for publication will simply not be accepted unless data and fully functional code are available. In other words, if the data and code are not public then the journals will not even consider the article for publication, except in very rare circumstances. This is simple, fair and transparent and works without any dissent. It also avoids any rancorous disagreements between journal and author after the event. Physical science journals are, by and large, far behind the econometricians on this score. While most have adopted one pious policy or another, giving the appearance of transparency on data and code, as we have seen in the unfolding of this story, there has been a near-complete failure to enforce these rules. This failure simply stores up potential problems for the editors: if an author refuses to release his data, the journal is left with an enforcement problem from which it is very difficult to extricate themselves. Their sole potential sanction is to withdraw the paper, but this then merely opens them up to the possibility of expensive lawsuits. It is hardly surprising that in practice such drastic steps are never taken. The failure of climatology journals to enact strict policies or enforce weaker ones represents a serious failure in the system of assurance that taxpayer-funded science is rigorous and reliable. Funding bodies claim that they rely on journals to ensure data availability. Journals want a quiet life and will not face down the academics who are their lifeblood. Will Nature now go back to Mann and threaten to withdraw his paper if he doesn’t produce the code for his confidence interval calculations? It is unlikely in the extreme. Until politicians and journals enforce the sharing of data, the public can gain little assurance that there is any real need for the financial sacrifices they are being asked to accept. Taking steps to assist the process of replication will do much to improve the conduct of climatology and to ensure that its findings are solidly based, but in the case of papers of pivotal importance politicians must also go further. Where a paper like the Hockey Stick appears to be central to a set of policy demands or to the shaping of public opinion, it is not credible for policymakers to stand back and wait for the scientific community to test the veracity of the findings over the years following publication. Replication and falsification are of little use if they happen after policy decisions have been made. The next lesson of the Hockey Stick affair is that if governments are truly to have assurance that climate science is a sound basis for decision-making, they will have to set up a formal process for replicating key papers, one in which the oversight role is peformed by scientists who are genuinely independent and who have no financial interest in the outcome.

Montford, Andrew (2011-06-06). The Hockey Stick Illusion (pp. 379-383). Stacey Arts. Kindle Edition.

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