October 2005 Archives

Dave Krantz pointed me to a paper by Kahan, Braman, Gastil, Slovic, and Mertz on "Gender, race, and risk perception: the influence of cultural status anxiety," which explores the "white male effect," which is the "tendency of white males to fear all manner of risk less than women and minorities," a pattern first noted by Slovic and others in the early 1990s. Finucane and Slovic (1999) wrote that “the white-male effect seemed to be caused by about 30 percent of the white male sample that judged risks to be extremely low.”

Here's the abstract of the new paper:

Why do white men fear various risks less than women and minorities? Known as the “white male effect,” this pattern is well documented but poorly understood. This paper proposes a new explanation: cultural status anxiety. The cultural theory of risk posits that individuals selectively credit and dismiss asserted dangers in a manner supportive of their preferred form of social organization. This dynamic, it is hypothesized, drives the white male effect, which reflects the risk skepticism that hierarchical and individualistic white males display when activities integral to their status are challenged as harmful. The paper presents the results of an 1800-person survey that confirmed that cultural worldviews moderate the impact of sex and race on risk perception in patterns consistent with status anxieties. It also discusses the implication of these findings for risk regulation and communication.

The paper is interesting, and I'm sympathetic to its general arguments--it certainly makes sense to me that risk perceptions, and perceptions about uncertainties in general, will be influenced by cultural values. But I have a couple of concerns relating to how the data were collected and analyzed.

The findings of the article come from regression analyses of responses to a national survey. They aksed people about their perceptions of risks of environmental danger, guns, and abortion. They also asked some cultural world view and personality questions, along with demographics. They found that the cultural worldview questions were predictive of risk attitudes.

I'm just a little worried that they may be measuring political views as much as risk attitudes. For example, one of the agree/disagree statements is "Women who get abortions are putting their health in danger." Statistically, my impression is that the health risk from abortion itself is low, but a person who opposes abortion might answer Yes to the question, on the grounds that a lifestyle associated with frequent abortions is risky. My point here is that the answer to the question itself could have a political twist to it. Although the question is nominally about risks, I don't know how much it's really telling us about risk perception.

I'm not saying that this is a devastating critique. Understanding the "white male effect" is a challenge, and cultural world view, etc., has got to be relevant. But this particular study maybe could be interpreted in other ways.

I was lucky enough to be a T.A. for Fred Mosteller in his final year of teaching introductory statistics at Harvard. He had taught for 30 years and told us that in different years he emphasized different material--he never knew what aspect of the course they would learn the most from, so each year he focused on what interested him the most.

Anyway, every week he would take his three T.A.'s to lunch to talk about how the course was going and just to get us talking about things. One day he asked us what we thought about some issue of education policy--I don't remember what it was, but I remember that we each gave our opinions. Fred then told us that, as statisticians, people are interested in our statistical expertise, not in our opinions. So in a professional context we should be giving answers about sampling, measurement, experimentation, data analysis, and so forth--not our off-the-cuff policy opinion, which are not what people were coming to us for.

I was thinking of this after reading David Kane's comment on Sam's link to an article about the book, The Bell Curve. David asked me (or Sam) to tell us what we really think about the Bell Curve. I can't speak for Sam, but I wouldn't venture to give an opinion considering that I haven't read the book. I'd like to think I'm qualified to make judgments about it, if I were to spend the effort to follow all the arguments--but it would take a lot of time, and my impression is that a bunch of scientists have already done so (and have come to various conclusions on the topic). I would imagine that I might be inclined to study the issue further if I were involved in a study evaluating educational policies, for example, but it hasn't really come up in any of my own research. (I did think that James Flynn's article on a related topic was interesting, but I don't even really know what are the key points of The Bell Curve are, so I wouldn't presume to comment.

Over the years, I've been distressed to see statistians and other academic researchers quoted as "experts" in the news media, even for subjects way out of their areas of expertise. It takes work to become an expert on a topic. Teaching classes in probability and statistics isn't always enough. As a reaction to this, I've several times said no to media requests on things that I'm not an expert on. (For example, when asked to go on TV to comment on something on the state lottery, I forwarded them to Clotfelter and Cook, two economists at Duke who wrote an excellent book on the topic.) Standards for blogs are lower than for TV, but still . . .

I spoke at Swarthmore College last week. Here are the abstracts and here are the talks: Mathematical vs. statistical models in social science (for the general audience) and Coalitions, voting power, and political instability (for math and stat majors).

Visiting the Swarthmore math dept was lots of fun. It's great to be at a place where teaching is taken seriously. The classrooms, student common areas, faculty common areas, and faculty offices were all near each other, and students were always walking by and dropping in to faculty offices. After my talk on the first day, there was a dinner, at which I sat at a table with several students. I was impressed at the level of discussion--it seemed to be a really intellectual place. (It also was fun, in a way, to eat dining hall food--I hadn't done that for many years!)

Class-participation activities

On the second day, I did a probability demo for the students in the math-stat course, and a statistics demo for the students in the intro stat course. The probability demo involved a jar of coins and culminates in an expected-monetary-value calculation that can be done by differentiating xp(x) (where p is the normal density function with a specified mean and variance); setting the derivative to zero reduces to solving a quadratic equation. The instructor for both classes the was Walter Stromquist, who did mathematics in the "real world" for many years as a consultant before coming to teach. While I was differentiating and solving the equation on the board, he quickly programmed the formula into a spreadsheet and computed the optimal solution before I could finish. For the second class, I did the real- and fake-coin-flips demo: while I was out of the room, each pair of students created either a sequence of 100 coin flips or a sequence of 100 1's and 0's that were supposed to be fake. Then I returned and was shown sequences in pairs, with my task being to tell the real and fake sequences apart. I'm embarrassed to say that I only got 4 out of the 5 pairs correct.

Mathtalk

Overheard in the hallway of the math department:

Teacher 1: When a proof has a gap, use L'Hopital's Rule.

Teacher 2: Everytime my lectures have a gap, I tell a joke.

Teacher 1: What happens if the joke has a gap?

I'm sorry. You come to this blog seeking deep thoughts and insight, and I give you links and rants. Or gratuitous plugs for things that appeal to me, which is what today's post contains. There's a new-ish magazine/literary journal called n+1. It's full of deep thoughts and insight on various topics, from travel to domestic violence to the vicious cycle that is dating. And it's called n+1--how cool is that?

I wish there were more connections between statistics departments and biostatistics departments. I've been working with survival data recently, and it's made me realize another gaping hole in my statistical knowledge base. It's also made me realize that I wish I knew more biostatisticians. And I'm one of the lucky ones, really, because Columbia has a biostatistics department and I do know some people there. Often when statistics and biostatistics departments don't have close connections, it's for understandable reasons. When I was in graduate school at Harvard, for example, the statistics and biostatistics departments were (still are, I guess) separated by the Charles River and it took a 45-minute bus ride to travel between the two. I almost never made that trip. Still, there are some great people in the Harvard Biostatistics Department and I'm sure I could have benefited from working with or taking classes from them. Here at Columbia, the biostatistics department is a subway ride away from the statistics department, and if you take the 1 train then there's that awful subway elevator to contend with (how on earth is that not a fire hazard?). Lots of universities don't have both statistics and biostatistics departments; of the ones that do there are some with close connections. I just wish that was the rule rather than the exception.

I spent too much of one day last week reading this article and everything it links to. Charles Murray, one of the authors of The Bell Curve, also has a piece in the August 2005 issue of Statistical Science called "How to Accuse the Other Guy of Lying with Statistics" (part of a special section "celebrating" the 50th anniversary of "How to Lie with Statistics"--it's a fun issue).

I haven't read The Bell Curve myself, so I better stop now.

In a comment here, Martin Termouth cited this report from Nature, "One in three scientists confesses to having sinned."

But what are these sins? Here's the relevant table:

This looks pretty bad, until you realize that the rarest behaviors, which are also the most severe, are at the top of the table. The #1 "sin," admitted-to by 15.5% of the respondents, is "Changing the design, methodology or results of a study in response to pressure from a funding source." But is that a sin at all? For example, I've had NIH submissions where the reviewers made good suggestions about the design or data analysis, and I've changed the plan in my resubmission. This is definitely "pressure"--it's not a good idea to ignore your NIH reviewers--but not improper at all.

From the other direction, as an NSF panelist I've made suggestions for research proposals, with the implication that they better think very hard about alternative designs or analyses if they want to get funding. This all seems proper to me. Of course, I agree that it's improper to change the results of a study in response to pressure. But, changing the design or methodology, that seems OK to me.

Now let's look at the #2 sin, "Overlooking others' use of flawed data or questionable interpretation of data." This is not such an easy ethical call. Blowing the whistle on frauds by others is a noble thing to do, but it's not without cost. My friend Seth Roberts has, a couple times, pointed out cases of scientific fraud (here's one example), and people don't always appreciate it. Payoffs for whistleblowing are low and the costs/risks are high, so I'd be cautious about characterizing "Overlooking other's use of flawed data..." as a scientific "sin."

Now, the #3 sin, "Cirumventing certain minor aspects of human-subjects requirements." I agree that this could be "questionable" behavior. Although I'm not quite sure if "circumventing" is always bad. It's sort of like the difference between "tax evasion" (bad) and "tax avoidance" (OK, at least according to Judge Learned Hand).

Taking out these three behaviors leaves 11.4%, not quite as bad as the "more than a third" reported. (On the other hand, these are just reported behaviors. I bet there's a lot more fraud out there by people who wouldn't admit to it in a survey.)

If you've read this far, here's a free rant for you!

P.S. When you click on a Nature article, a pop-up window appears, from "c1.zedo.com", saying "CONGRATULATIONS! YOU HAVE BEEN CHOSEN TO RECEIVE A FREE GATEWAY LAPTOP . . . CLICK HERE NOW!." Is this tacky, or what? I thought the British were supposed to be tasteful!

Eric Oliver is speaking todayin the American Society and Politics Workshop on "fat politics." Here's the paper and here are some paragraphs from it:

In truth, the only way we are going to “solve” the problem of obesity is to stop making fatness a scapegoat for all our ills. This means that public health officials and doctors need to stop making weight a barometer of health and issuing so many alarmist claims about the obesity epidemic. This also means that the rest of us need to stop judging others and ourselves by our size.

Such a change in perspective, however, may be our greatest challenge. Our body
weight and fatness is a uniquely powerful symbol for us – something we feel we should
be able to control but that often we can’t. As a result, obesity has become akin to a
sacrificial animal, a receptacle for many of our problems. Whether it is our moral
indignation, status anxiety, or just feelings of general powerlessness, we assume we can
get a handle on our lives and social problems by losing weight. If we can only rid
ourselves of this beast (that is, obesity), we believe we will not only be thin, but happy,
healthy, and righteous. Yet, as with any blind rite, such thinking is a delusion and
blaming obesity for our health and social problems is only going to cause us more injury
over the long haul.

So how might we change our attitudes about obesity and fat? As with any change
in perspective, the first place we must begin is in understanding why we think the way we
do. In the case of obesity, we need to understand both why we are gaining weight and,
more importantly, why we are calling this weight gain a disease. In other words, if we
are to change our thinking about fat, we need to recognize the real sources of America’s
obesity epidemic.

Oliver continues:

Monday talk (for general audience):

Mathematical vs. statistical models in social science

Mathematical arguments can give insights into social phenomena but, paradoxically, tend to give qualitative rather than quantitative predictions. In contrast, statistical models, which often look messier, can introduce new insights. We give several examples of interesting, but flawed, mathematical models for examples including political representation, trench warfare, the rationality of voting, and the electoral benefits of moderation. We consider ways in which these models can be improved in these examples. We also discuss more generally why mathematical models might be appealing and why they commonly run into problems.

Tuesday talk (for math/stat majors and other interested parties):

Coalitions, voting power, and political instability

We shall consider two topics involving coalitions and voting. Each topic involves open questions both in mathematics (probability theory) and in political science.
(1) Individuals in a committee or election can increase their voting power by forming coalitions. This behavior yields a prisoner's dilemma, in which a subset of voters can increase their power, while reducing average voting power for the electorate as a whole. This is an unusual form of the prisoner's dilemma in that cooperation is the selfish act that hurts the larger group. The result should be an ever-changing pattern of coalitions, thus implying a potential theoretical explanation for political instability.
(2) In an electoral system with fixed coalition structure (such as the U.S. Electoral College, the United Nations, or the European Union), people in diferent states will have different voting power. We discuss some flawed models for voting power that have been used in the past, and consider the challenges of setting up more reasonable mathematical models involving stochastic processes on trees or networks.

If people want to read anything beforehand, here's some stuff for the first talk:

http://www.stat.columbia.edu/~gelman/research/unpublished/trench.doc
http://www.stat.columbia.edu/~gelman/research/unpublished/rational_final5.pdf
http://www.stat.columbia.edu/~gelman/research/published/chance.pdf

and here's some stuff for the second talk:

http://www.stat.columbia.edu/~gelman/research/published/blocs.pdf
http://www.stat.columbia.edu/~gelman/research/published/STS027.pdf
http://www.stat.columbia.edu/~gelman/research/published/gelmankatzbafumi.pdf

Gary writes about the social science of architecture, after being deeply involved in the design and construction of a new office building. Key quote:

Ultimately the goal of this particular $100M-plus building, and of most buildings built by universities, is not only to create beautiful surroundings but also to increase the amount of knowledge created, disseminated, and preserved (my summary of the purpose of modern research universities). . . . As such, some systematic data collection could have a considerable impact on this field. Do corridors or suites make the faculty and students produce and learn more? Does vertical circulation work as well as horizontal? Should we put faculty in close proximity to others working on the same projects or should we maximize interdisciplinary adjacencies? . . .

From another perspective, and speaking as a consumer rather than a designer of architecture, I'd be interested in a study of the incentives to architects. My completely unscientific impression is that a lot of buildings that were built during the 1960s and 1970s were poorly functional--often too hot or too cold, hard to find the entrances, hard to find your way around the building, and not making good use of the available land. Since then, public buildings have improved. Anyway, I wonder about the incentives for these architects. Do they advance in their career by building interesting but non-functional buildings? What is their incentive to build something that can work well?

Gary's proposal, of taking lots of outcome measurements on building use, could be helpful for the reasons he states (to evaluate architectural plans) but also as a motivation, even as a reminder to builders that these outcomes are relevant goals. (Just as, by analogy, student evaluations put some pressure on teachers and remind us not to forget about the students in our classes.) Feedback is good.

Also, regarding Gary's proposed study of office buildings, you could also make a study of private houses. This gives you a potentially huge N, and also raises issues of public/private priorities (lawns vs. parks, etc.). I've seen a million statistical papers on real estate prices, but little or nothing on outcomes relating to the houses as experienced by the residents..

I went to Radio Shack the other day and bought a telephone answering machine.

Q: Did I want to buy the extended warranty for $5.99? [Students: figure this one out before continuing...]

I can't believe Nixon won. I don't know anybody who voted for him. -- mistakenly attributed to Pauline Kael, 1972

It evidently irritates many liberals to point out that their party gets heavy support from superaffluent "people of fashion'' and does not run very well among "the common people.'' -- Michael Barone, 2005

Both these quotes correspond to political misunderstandings which I thiink can be attributed to a well-known cognitive bias.

First-order and second-order availability biases

Psychologists have studied the "availability bias"--the phenomenon that people tend to overweight their own experiences when making decisions or judging rates or probabilities. I was thinking about this, in regard to political commentators who are trying to understand who's voting for whom in presidential elections.

In this case, we could speak of first-order and second-order availability biases. A national survey of journalists found that about twice as many are Democrats as Republicans. Presumably their friends and acquaintances are also more likely to support the Democrats, and a first-order availability bias would lead a journalist to overestimate the Democrats' support in the population--as in the above quote that had been attributed to Pauline Kael.

However, political journalists are well aware of the latest polls and election forecasts and are unlikely to make such an elementary mistake. However, they can well make the second-order error of assuming that the correlations they see of income and voting are representative of the population. Weaver et al. (2003) found that 90% of journalists are college graduates and have moderately high incomes--so it is natural for them to think that they and their friends represent Democrats as a whole. Michael Barone, for example, although no liberal himself, probably knows many affluent liberal Democrats and then, from a second-order availability bias, imputes an incorrect correlation of income and Democratic voting to the general population. (Just to be clear on this point: richer voters tend to support the Republicans. Barone, should know better but was, I believe, faked out by a second-order availability bias. These cognitive biases can fake out the best of us--they come from inside our head and avoid our usual barriers of skepticism.)

When considering income and voting, the second-order availability bias is exacerbated by geographic patterns

Another form of availability bias is that the centers of national journalistic activity are relatively rich states including New York, California, Maryland, and Virginia. Once again, the journalists--and, for that matter, academics--avoid the first-order availability bias: unlike "Pauline Kael" (in the mistakenly-attributed quote), they are not surprised that the country as a whole votes differently from the residents of big cities. But they make the second-order error of too quickly generalizing from the correlations in their states. It turns out (as we show in our forthcoming paper) that richer counties tend to support the Democrats within the "media center'' states but not, in general, elsewhere. And richer voters support the Republicans just about everywhere, but this pattern is much weaker--and thus easier to miss--within these states.

Much has been written in the national press about the perils of ignoring "red America'' but these second-order availability biases have done just that, in a more subtle way.

Tyler Cowen links to Matt Yglesias linking to a quote from Frans De Waal, who's writing about a method of evaluating conversations using low-frequency voice patterns. Anyway, here's the relevant paragraph from De Waal:

The same spectral analysis has been applied to televised debates between U.S. presidential candidates. In all eight elections between 1960 and 2000 the popular vote matched the voice analysis: the majority of people voted for the candidate who held his own timbre rather than the one who adjusted.

But the elections of 1960, 1968, 1976, and 2000 were essentially tied. You get no credit for predicting the "winner" in any of these, any more than you would get credit for correctly predicting the outcome of a coin flip. (This is a point I made back in 1992 in my review of a book on forecasting elections.)

Anyway, I'm not trying to criticize (or evaluate in any way) what De Waal is doing--let's just not ovestate the evidence here.

Jens Hainmueller refers to a paper by David Lee, "Randomized experiments from non-random selection in U.S. House elections." In the paper, Lee uses a regression discontinuity analysis to compare election outcomes in districts that, two years earlier, were either barely won by Democrats or barely won by Republicans. The difference between these districts in the next election can be identified as the causal effect of the incumbent party--that is, the difference it makes, having a Democrat or a Republican running, in otherwise nearly-identical districts.

Lee's analysis is fine, and he has a nice picture on page 33 of his paper showing his model and how his estimate compares to that of Gelman and King (1990). However, he is wrong to label what he is estimating as "the electoral advantage to incumbency." He is more precise in Section 3.5 and Appendix B of his paper, when he refers to his estimate of "the incumbent party advantage." The difference is, as Lee makes clear in his paper, that in a hypothetical world in which incumbency itself were worth nothing--in which a Democrat in an open seat would run as well as a Democrat who is an incumbent--you could still have a nonzero incumbent party advantage, if voters preferred to stick with the same party they had before. So I agree with the message of Lee, that both these things--the incumbent party advantage and the incumbency advantage--are interesting. As Gary and I discuss on page 1153 in our 1990 paper, yet another quantity of interest is the personal incumbency advantage, a quantity that has also been studied by Cox, Katz, Ansolabehere, and others.

On a related point, I think Lee is misleading when he says (on page 28) that "the regression discontinuity estimates cannot be recovered from a Gelman-King type analysis." I mean, yes, we use a linear model on vote proportions, and he has a model of probabilities. But we do have an incumbent party effect--it is the coefficient of the incumbent party indicator P_2 in our model--so we did in fact estimate this (within the context of a linear model).

One other, more technical issue: there is a lot of information in the actual vote shares received by the candidates, which is why political scientists typically model these directly. Modeling vote shares gives you the efficiency to get separate estimates for each election year and thus study time trends. I understand the appeal of simply looking at winning and losing, but there is much to be learned by studying vote shares.

In summary, I like Lee's paper, and it's good to see connections between different social sciences. For the particular example of incumbency advantage, I'd have more trust in simple regression estimators, separating the effects of incumbent party (P_i) and incumbency (I_i) as discussed in our 1990 paper and in Lee's Appendix B. Or, to go in new directions, using the Bayesian method of Gelman and Huang (2006, to appear). But it can't hurt to have new methods, and for other problems where the linear model doesn't work so well, I could see Lee's method providing a real advance.

Statisticians continue to be in demand, especially those who are interested in social science and policy applications. From Susan Paddock at RAND:

Today I came across a paper in my files, "On a limiting process which asymptotically produces f^{-2} spectral density" from 1962 by Hirotugu Akaike (most famous for his information criterion). The paper has a great opening paragraph:

In the recent papers in which the results of the spectral analyses of roughnesses of runways or roadways are reported, the power spectral densities of approximately the form f^{-2} (f: frequency) are often treated. This fact directed the present author to the investigation of the limiting process which will provide the f^{-2} form under fairly general assumptions. In this paper a very simple model is given which explains a way how the f^{-2} form is obtained asymptotically. Our fundamental model is that the stochastic process, which might be considered to represent the roughness of the runway, is obtained by alternative repetitions of roughening and smoothing. We can easily get the limiting form of the spectrum for this model. Further, by taking into account the physical meaning of roughening and smoothing we can formulate the conditions under which this general result assures that the f^{-2} form will eventually take place.

It's a cool paper, less than 5 pages long. Something about this reminds me of Mandelbrot's early papers on taxonomy and Pareto distributions, written about the same time.

In a recent article in the New York Review of Books (see also here), Freeman Dyson writes,

Great scientists come in two varieties, which Isaiah Berlin, quoting the seventh-century-BC poet Archilochus, called foxes and hedgehogs. Foxes know many tricks, hedgehogs only one. Foxes are interested in everything, and move easily from one problem to another. Hedgehogs are interested only in a few problems which they consider fundamental, and stick with the same problems for years or decades. Most of the great discoveries are made by hedgehogs, most of the little discoveries by foxes. Science needs both hedgehogs and foxes for its healthy growth, hedgehogs to dig deep into the nature of things, foxes to explore the complicated details of our marvelous universe. Albert Einstein was a hedgehog; Richard Feynman was a fox.

This got me thinking about statisicians. I think we're almost all foxes! The leading stasticians over the years all seem to have worked on lots of problems. Even when they have, hedghehog-like, developed systematic ideas over the years, these have been developed in a series of applications. It seems to be part of the modern ethos of statistics, that the expected path to discovery is through the dirt of applications.

I wonder if the profusion of foxes is related to statistics's position, compared to, say, physics, as a less "mature" science. In physics and mathematics, important problems can be easy to formulate but (a) extremely difficult to solve and (b) difficult to understand the current research on the problem. It takes a hedgehog-like focus just to get close enough to the research frontier that you can consider trying to solve open problems. In contrast, in statistics, very little background is needed, not just to formulate open problems but also to acquire many of the tools needed to study them. I'm thinking here of problems such as how to include large numbers of interactions in a model. Much of the progress made by statisticians and computer scientists on this problem has been made in the context of particular applications.

Going through some great names of the past:

Don Rubin published an article in 2002 on "The ethics of consulting for the tobacco industry." Here's the article, and here's the abstract:

This article describes how and why I [Rubin] became involved in consulting for the tobacco industry. I briey discuss the four relatively distinct statistical topics that were the primary focus of my work, all of which have been central to my published academic research for over three decades: missing data; causal inference; adjustment for covariates in observational studies; and meta-analysis. To me [Rubin], it is entirely appropriate to present the application of this academic work in a legal setting.

My thoughts:

I respect what Don is saying here--I don't think he'd do this sort of consulting without thinking it through. At the same time, I think there are a couple of complications not mentioned in his article.

Paul Gustafson and Sander Greenland have a preprint entitled, "The Performance of Random Coefficient Regression in Accounting for Residual Confounding." From their paper:

The problem studied in detail by Greenland (2000) involves a case-control study of diet, food constituents, and breast cancer. The exposure variables are intakes of 35 food constituents (nutrients and suspected carcinogens), each of which is computed from responses to an 87-item dietary questionnaire. An analysis based on the 35 food constituents alone assumes that the 87 diet items have no effect beyond that mediated through the food constituents. Greenland (2000) comments that this is a strong and untenable assumption. As an alternative he included both the food constituents and the diet items in a logistic regression model for the case-control status, while acknowledging that this model is formally nonidentified since each food constituent variable is a linear combination of the diet variables. To mitigate the lack of identifiability, a prior distribution is assigned to the regression coefficients for the diet variables, i.e., random coefficient regression is used. The prior distribution has mean zero with small variance, chosen to represent the belief that these coefficients are likely to be quite small typically, as they represent `residual confounding’ effects of diet beyond those represented by the food constituents. Greenland argued that, however questionable this prior may be, it is surely better than the standard frequentist analyis of such data, which omits the diet variables entirely – equivalent to using the random-coefficient model with a prior distribution that has variance (as well as mean) zero.

I have long felt that hierarchical modeling is the way to go in regression with large numbers of related predictors, but I was not familiar with the Greenland (2000) paper. Section 5.2.3 of my 2004 Jasa paper on parameterization and Bayesian modeling presents a similar idea, but I've never actually carried it out in a real application. So I'd be interested in seeing more about Greenland's example.

P.S. I like the following quote in the abstract of Greenland's paper:

The argument invokes an antiparsimony principle attributed to L. J. Savage, which is that models should be rich enough to reflect the complexity of the relations under study. It also invokes the countervailing principle that you cannot estimate anything if you try to estimate everything (often used to justify parsimony). Regression with random coefficients offers a rational compromise . . .

This accords with my views on parsimony and inference (see also here and here).

P.P.S. On a technical level, I'm disturbed that Gustafson and Greenland use inverse-gamma prior distributions for their variance parameters. I think this is too restrictive as a parametric family. Ironically, the family of prior distributions I've proposed has the same mathematical form as the multiplicative models that can be used for varying coefficients.

In a recent article in the New York Review of Books, Freeman Dyson quotes Richard Feyman:

No problem is too small or too trivial if we really do something about it.

This reminds me of the saying, "God is in every leaf of every tree," which I think applies to statistics in that, whenever I work on any serious problem in a serious way, I find myself quickly thrust to the boundaries of what existing statistical methods can do. Which is good news for statistical researchers, in that we can just try to work on interesting problems and the new theory/methods will be motivated as needed. I could give a zillion examples of times when I've thought, hey, a simple logistic regression (or whatever) will do the trick, and before I know it, I realize that nothing off-the-shelf will work. Not that I can always come up with a clean solution (see here for something pretty messy). But that's the point--doing even a simple problem right is just about never simple. Even with our work on serial dilution assays, which is I think the cleanest thing I've ever done, it took us about 2 years to get the model set up correctly.

As the saying goes, anything worth doing is worth doing shittily.

Alex Tabarrok writes, regarding the example in Section 3 of this paper,

Another nice illustration of the importance of weighting comes from high-stakes schemes that reward schools for improving test scores. North Carolina, for example, gives significant monetary awards to schools that raise their grades the most over the year. The smallest decile of schools has been awarded the highest-honors (top-25 in the state) 27% of the time while schools in the largest decile have received that honor only about 1% of the time. Students (and parents) are naturally led to believe that small schools are better. But just as with the cancer data, the worst schools also come from the smallest decile. The reason, of course, is the same as with the cancer data small changes in incoming student cohorts make the variance of the score changes much larger at the smaller schools. There are some nice graphs and discussion in

Kane, T. and D. O. Staiger. 2002. The Promise and Pitfalls of Using Imprecise School Accountability Measures. Journal of Economic Perspectives 16 (4):91-114.

It's scary to think of policies being implemented based on the fallacy of looking at the highest-ranking cases and ignoring sample size. But most of my students every year get the cancer-rate example wrong--that's one reason it's a good example!--so I guess it's not a surprise that policymakers can make the mistake too. And even though people point out the error, it can be hard to get the message out. (For example, Kane and Staiger hadn't head of my paper with Phil Price on the topic, and until recently, I hadn't heard of Kane and Staiger's paper either.)

I just came back from a talk by Jere Behrman on "What Determines Adult Cognitive Skills? Impacts of Pre-School, School-Years and Post-School Experiences in Guatemala." Here's the paper.

It was all interesting, but what confused me here, as in other talks of this type, was the interpretation of regressions controlling for several variables that are sequential in time. This particular example was a longitudinal study of about 1500 people, looking at adult cognitive outcomes and including, as predicotrs, measures of health at age 6, years of schooling, and work after school was over. It's tricky to interpret the coefficient of pre-school health in this regression as a "treatment effect" since it can affect the other predictors. People at the seminar were talking along the lines of "causal pathways" but this always confuses me too. A simple response is to follow the basic advice of not controlling for post-treatment outcomes, but doing such an analysis wouldn't address some of the questions the researchers were trying to study here.

So I'm left simply confused. I'm not trying to be critical of this paper, since I'm not really offering an alternative. But I'm not quite sure how to interpret all these regression coefficients. (Even setting aside the issues involving instrumental variables, which are used in this study also.) I'm just a little stuck here.

Paul Del Piero, a student at Pomona College, did a study of four redistricting plans in California. He uses uniform partisan swing (which can be viewed as an approximation to the method used by the Judgeit program developed by Gary King and myself) to estimate seats-votes curves. Here's his paper, here are the appendices for the paper, and here's the abstract.

I also have one comment of my own, which I'll give after Paul's abstract:

Could it make sense for the Republicans to support geographically-localized policies that help the poor and geographically-diffuse policies that help the rich?