Statistical Modeling, Causal Inference, and Social Science

"Science revolves around the discovery of new cause-effect relationships but the entire statistics literature says almost nothing about how to do this."

2009-11-19T16:13:32Z

Seth writes:

Is this a fair statement, do you think?
Science revolves around the discovery of new cause-effect relationships but the entire statistics literature says almost nothing about how to do this.

It's part of an abstract for a talk I [Seth] will give at the ASA conference next July. Haven't submitted the abstract yet so can revise it or leave it out.

My reply: This seems reasonable to me.

You could clarify that the EDA literature is all about discovery of new relationships but with nothing about causality, while the identification literature is all about causality but nothing about the discovery of something new.

]]> What literature there is on discovery of new causal relationships comes from structural equation modeling (also called graphical modeling), but this work is not particularly exploratory (it's all about discovering relationships in a pre-specified set of variables) and there's a lot of debate about how causal it is. (The proponents of structural equation modeling and graphical modeling think these tools can be used to discover causality from just about any observational data, but others are skeptical of these claims--rightfully skeptical, in my opinion.)

My point here is not to bash structural equation modeling, just to say that, unless you happen to be a strong believer in that family of methods, Seth's statement is pretty much correct. And an interesting point it is. It might very well be that statistics just isn't suited to such questions--I think we make a lot of useful progress in descriptive analysis of the Red State, Blue State variety (or of the identifying-genes-associated-with-diseases variety) but it's worth at least occasionally thinking about the deeper questions.

Senators and health care; also a discussion of pretty statistical graphics

2009-11-19T13:16:01Z

Nate, Daniel, and I have an op-ed in the Times today, about senators' positions and state-level opinion on health care. We write:

Lawmakers' support for or opposition to reform generally has less to do with the views of their constituents and more to do with the issue of presidential popularity. . . .
For instance, Senator Blanche Lincoln, a Democrat who has been a less-than-strong supporter of the present health care bill, recently told The Times, "I am responsible to the people of Arkansas, and that is where I will take my direction." But where does she look for her cue? Hers is a poor state whose voters support health care subsidies six percentage points more than the national average. On the other hand, Mr. Obama got just 40 percent of the vote there.

Likewise, in Louisiana, where the Annenberg surveys showed health care reform to be popular but where Mr. Obama is not, the Democrats are not assured of Mary Landrieu's vote. . . .

Here's our graph that makes this point:

]]>

In putting together the op-ed, the art dept at the Times made some changes (with our guidance and approval). Here's what they made:

Much nicer than our original, I have to say!

We also look at public opinion within states:

Using a statistical method called multilevel regression and post-stratification, we also mapped opinion on health care, breaking down voters by age, family income and state. We're used to thinking about red states and blue states, but the geographic variation is dwarfed by the demographic patterns: younger, lower-income Americans strongly support increased government spending on health care, while elderly and well-off Americans are much less supportive of the idea.

And here are the maps that tell the story:

Again, the Times improved it (saving space slightly by combining the two highest income categories):

The Times version is not just more attractive; it's also easier to read, I think, in the sense of being more self-contained. (I still prefer our color scheme, though.)

Summary on the politics

Swing senators' positions on health care are often presented in terms of worries about voter attitudes in the senators' home states. Overall I don't think this fits the data. Attitudes on health care vary more consistently by age and income than by state (compare to our graphs of ideology and partisanship), and constituents' views on health care are not a strong predictor of senators' stances.

Public opinion is certainly relevant to the health care debate, but not in the direct senator-follows-the-state way that it is sometimes imagined.

Summary on the graphics

I liked our graphs, but the Times versions are better. Our graphs took months of effort, but the Times versions were not immediate either. We had to go back and forth several times to get the clarity we all wanted. I'd like to think, though, that our effort was not wasted: by being able to make a bunch of graphs that were informative for us, we were able to home in on the story. At that point, the graphics professionals helped us to do better.

It's tougher to make graphs for a newspaper than for a book, scholarly journal, or even a blog, I think. Even beyond the different audiences, a newspaper graph really has to be self-contained. In a book or article I can accompany the graph with a caption, and I make full use of captions to make each graph reasonably self-contained (to the benefit of people such as myself who jump from graph to graph when reading), and in a blog I can put whatever I want right below the graph. But in the newspaper, the graph really has to stand alone and with minimal captioning.

Statfight!

2009-11-19T09:38:00Z

Fun stuff.

They call me Dear Abby, or, This might at first seem like a pointless tautological exercise, but actually I think it can lead you forward

2009-11-18T20:50:30Z

Daniel Corsi writes:

I am a PhD student in epidemiology at McMaster University and I am interested in exploring how characteristics of communities are related to child health in developing countries.
I have been using multilevel models to relate physical characteristics of communities such as the number of schools, health clinics, sanitation facilities etc to child height for age and weight for age using observational/survey data.

I have several questions with regards to the group (community-level) level predictors in these models.

]]> 1. My first question is about interpretation of the group-level coefficients. I have found some modest coefficients around the order of .13 (se .05) on several community-level variables (i.e. number of schools) predicting child height for age in standard deviation units. I know from your ARM book that we should be interpreting these coefficients cautiously especially in observational studies. My question is does this apply to the interpretation of all variables or just variables created by aggregating an individually-measured variable to the group level?

2. The second and related point is do you have any suggestions on combining several predictors together at the group level? I am wondering if it is more useful to look at the effects for several variables related to schools, health clinics, other services in separately or combine these variables in to some form of an index to include in one model. These variables are typically highly correlated and therefore it doesn't seem to make sense to me to include several individual variables in the same model without combining into some form of a 'total' community facility index - but I haven't found much in the literature about this point.

3. And the last question I have for you is - Is it even reasonable to be looking at group level influences on child health in this way? And would you suggest controlling for other individual-level predictors of child health for instance household socioeconomic status or mother education? As community-facilities are likely related to these intermediating variables which are stronger predictors of child health, any potential effect of the community environment could be masked by for instance the household SES. It is also likely that it is the high-SES areas that will have access to better facilities so I am having a difficulty with this issue.

I am not necessarily looking for causal effects, although it is helpful to think this way. What I am really interested in is what can be learned about community-level characteristics and their influence on child health parameters by using multilevel models, and is there a way to try and understand this that doesn't require causal interpretation of the group-level coefficients?

Thank you for your help with this, I realize that it is a potentially a complex issue, but I haven't found many references to this point, if you have any advice or references that would be very helpful.

My reply:

1. It's always a good idea to be careful. When I'm stuck on causal interpretations, I go back to descriptive language, for example: Comparing two kids of the same race, birth order, socioeconomic status, etc., but one kid lives in neighborhood X (which is 1 sd above the mean on #schools but at the mean level on all other neighborhood-level characteristics) and the other kid lives in neighborhood Y (which is 1 sd below the mean on #schools but at the mean level on all other neighborhood-level characteristics). Based on the model, you'd expect the kid in neighborhood Y to differ by ** much from the kid in neighborhood X.

This might at first seem like a pointless tautological exercise, but actually I think it can lead you forward. First, it gets you thinking about what does it mean for a neighborhood to be 1 sd above or 1 sd below the mean on a given characteristic. Second, it pushes you to think about the individual neighborhoods, to give you a sense of what these statistical results are really saying. Third, it gets you thinking about correlations between the predictors, Does it really make sense to compare two neighborhoods that differ in #schools but are identical in all other ways, or would it be better to compare neighborhoods that, more realistically, differ in many dimensions?

2. When combining predictors, I'm a big fan of simple averages, as discussed in chapter 4 of ARM. The same reasoning goes for group-level predictors. You just want to think a bit about the scaling.

3. I don't have any great answers here, but if you're thinking causally--and you should be, I'm sure--it helps to visualize some potential interventions and think about how they'd trickle down through the predictors in your models. Also think of some hypothetical experiments or observational studies you'd ideally like to do, then see if you can do some modeling to do your best job to fill in the gaps needed to make the inferences you're interested in.

P.S. Hey, maybe that should be my statistical motto: "This might at first seem like a pointless tautological exercise, but actually I think it can lead you forward"!

Clearing up some misconceptions about Bayesian statistics

2009-11-18T12:03:10Z

I was checking out the comments at my bloggingheads conversation with Eliezer Yudkowsky, and I noticed the following, from commenter bbbeard:

My sense is that there is a fundamental sickness at the heart of Bayesianism. Bayes' theorem is an uncontroversial proposition in both frequentist and Bayesian camps, since it can be formulated precisely in terms of event ensembles. However, the fundamental belief of the Bayesian interpretation, that all probabilities are subjective, is problematic -- for its lack of rigor. . . .

]]> One of the features of frequentist statistics is the ease of testability. Consider a binomial variable, like the flip of a fair coin. I can calculate that the probability of getting seven heads in ten flips is 11.71875%. I can check this, first of all, with a computer program that generates random numbers uniformly in [0,1) in groups of ten, and keeping tabs on what fraction of samples have exactly seven numbers less than 0.5. Obviously I can do this for any (m,n). I can also take a coin and flip it many times and get an empirical approximation to 11.71875%. At some point a departure from the predicted value may appear, and frequentist statistics give objective confidence intervals that can precisely quantify the degree to which the coin departs from fairness. . . . What is unclear to me is how a Bayesian would map out an experiment, either numerical or empirical, to demonstrate the posterior distribution in the unknown unfair coin experiment. That's why I ask, "what does the posterior distribution mean"? . . . The Bayesian interpretation is certainly not what we use in physics. Suppose we lived at a time before the speed of light was measured accurately. You could poll a bunch of people, even "experts", and get a range of guesses about the value of the speed of light. A Bayesian would construct a prior from this information. But what happens when you go do the experiment? . . .

I don't know that any readers of this blog will need an answer to these questions, but just quickly:

1. No, Bayesian probabilities don't have to be subjective. See chapter 1 of Bayesian Data Analysis for discussion and examples.

2. Bayesian models can indeed be tested. See chapter 6 of Bayesian Data Analysis.

3. Probability distributions in physics are not so clear as you might think. See the bottom half of page 7 in my Bayesian Analysis discussion here.

OK, I think that just about covers it.

P.S. These definitions (from pages 1-2 of this article) may also be of help:

"Bayesian inference" represents statistical estimation as the conditional distribution of parameters and unobserved data, given observed data. "Bayesian statisticians" are those who would apply Bayesian methods to all problems. (Everyone would apply Bayesian inference in situations where prior distributions have a physical basis or a plausible scientific model, as in genetics.) "Anti-Bayesians" are those who avoid Bayesian methods themselves and object to their use by others.

"What's a statistician? An accountant without the laughs."

2009-11-17T21:11:59Z

Andrew Roberts writes:

I teach political science at Northwestern. I have a book coming out with U of Chicago Press called "The Thinking Student's Guide to College" and I wanted to ask you a question about one part.
I have a section where I advocate a few "neglected majors". One of them is statistics. I wrote the following (see below) about statistics, but it seems a little dull to me. I'd be curious if you would add anything that would make the major seem more attractive. (FYI, the other neglected majors are linguistics, regional studies, and sociology).

To fully understand just about any phenomenon in the world, from atoms to people to countries, you need a grasp of statistics. Statistics teaches you how to measure quantities, collect data, and then draw inferences from that information. Though this might sound boring, these tasks are necessary to explain most of the forces affecting our lives, whether the workings of markets, the movement of public opinion, or the spread of disease. Not only does a statistics major give you the skills to answer these questions, it is also extremely marketable. There is hardly a firm which could not benefit from a trained statistician, and statisticians are just as desirable for public interest groups hoping to help the disadvantaged. And if you worry that you are not the math type, statistics is considerably less demanding than a pure math major and does more to help you understand the real world in all its complexities.

"Considerably less demanding than a pure math major," huh? OK, OK . . .

My main suggestion would be to be less apologetic. No need to say "Though this might sound boring"!

Perhaps some of you have specific suggestions for Andrew Roberts for his book?

Adaptively scaling the Metropolis algorithm using expected scaled jumped distance

2009-11-17T17:01:20Z

In the spirit of Christian Robert, I'd like to link to my own adaptive Metropolis paper (with Cristian Pasarica):

A good choice of the proposal distribution is crucial for the rapid convergence of the Metropolis algorithm. In this paper, given a family of parametric Markovian kernels, we develop an adaptive algorithm for selecting the best kernel that maximizes the expected squared jumped distance, an objective function that characterizes the Markov chain. We demonstrate the effectiveness of our method in several examples.

The key idea is to use an importance-weighted calculation to home in on a jumping kernel that maximizes expected squared jumped distance (and thus minimizes first-order correlations). We have a bunch of examples to show how it works and to show how it outperforms the more traditional approach of tuning the acceptance rate:

Regarding the adaptivity issue, our tack is to recognize that the adaptation will be done in stages, along with convergence monitoring. We stop adapting once approximate convergence has been reached and consider the earlier iterations as burn-in. Given what is standard practice here anyway, I don't think we're really losing anything in efficiency by doing things this way.

Completely adaptive algorithms are cool too, but you can do a lot of useful adaptation in this semi-static way, adapting every 100 iterations or so and then stopping the adaptation when you've reached a stable point.

The article will appear in Statistica Sinica.

Alan Abramowitz on politicians and ideological conformity

2009-11-17T13:33:49Z

In response to my note on the limited ideological constraints faced by legislators running for reelection, Alan Abramowitz writes:

I [Abramowitz] agree--although they probably have less leeway now than in the past due to growing pressure toward ideological conformity within parties, especially GOP. But one thing that struck me as very interesting in your graph is that it looks like the advantage of a moderate voting record is considerably smaller now than it used to be, down from over 4 percentage points in the 1980s to maybe 1.5 points on average now. It suggests to me that the electorate has become increasingly partisan and that fewer voters are going to defect to an incumbent from the opposing party regardless of voting record. This could reflect more concern among voters with party control of Congress itself. Along these lines, one thing I've found in the NES data is a growing correlation between presidential job evaluations and voting for both House and Senate candidates over time.

My reply: Yes, that makes sense. The trend is suggestive although (as you can see from the error bars) not statistically significant. Recently I have not had my thoughts organized enough to write any articles on this stuff, but it feels good to at least post these fragments for others to chew on.

More on risk aversion etc etc etc

2009-11-16T21:17:27Z

A correspondent writes:

You may be interested in this article by Matthew Rabin which makes the point that you make in your article: if you are an expected utility maximizer then turning down small actuarially unfair bets (e.g. 50% win $120; 50% lose $100) implies that you would never accept a bet where could lose $1000 (even if you might win an infinite amount of money). (But proved in more generality).
This was taught to me in the first year of my econ phd program (which I'm currently in!) as why you probably don't want to extrapolate from decisions over small bets to risk aversion in general, not as why we should throw out risk aversion and expected utility maximization completely. Of course, decision theorists do all kinds of things to try to "fix" this problem.

My reply: Yitzhak (as we called him in high school) wrote his paper after mine had appeared; unfortunately my article was in a statistics journal and he had not heard about it. (This was before I could publicize everything on the blog. And, even now, I think a few papers of mine manage to get out there without being noticed.)

I'm glad they teach this stuff in grad schools now--although, in a way, this still proves my point, in that the nonlinear-utility-function-for-money model is still considered such a standard that they feel the need to debunk it.

My correspondent replied: "I wouldn't call it a debunking....we still go on to use it as the workhorse model in everything we do...."

I think there are good and bad things about this "workhorse model":

]]> I think utility theory is great, both in theory and even in practice (which is why I devoted a chapter of Bayesian Data Analysis to it). And I have no problem with the study of risk aversion--that is, of the psychological/economic phenomenon of aversion to risk. I also think it's a good idea to study aversion to loss (not the same thing as risk, for example people don't seem to even like to lose $10, but that's hardly a "risk" in the usual sense of the word) and aversion to uncertainty (as in the $20/30/40 example). All three of these phenomena seem interesting to me, and important enough that it's worth keeping them as three separate concepts. Heck, I even like the game Risk.

But . . . I think that equating risk aversion to the declining utility of money is a mistake that doesn't help anybody. Given the well-known phenomenon of uncertainty aversion (even apart from loss aversion or risk aversion), I don't think it makes sense to use people's preferences over gambles, at whatever scale, to try to assess their utility functions.

I'm sure that there are lots of useful tools that people have for addressing these problems in applied economic analysis; as noted above, my frustration comes from always having to clear the air about risk aversion, uncertainty aversion, etc. I really think the term "risk aversion" does more harm than good, by leading people to think that there's one single concept that handles all these different psychological/economic phenomena.

Compact districts and Republican bias: further discussion from Michael McDonald

2009-11-16T21:16:44Z

Here.

"Finding signal from noise": Dr. Bancel responds

2009-11-16T19:49:38Z

The other day I commented on an article by Peter Bancel and Roger Nelson that reported evidence that "the coherent attention or emotional response of large populations" can affect the output of quantum-mechanical random number generators.

I was pretty dismissive of the article; in fact elsewhere I gave my post the title, "Some ESP-bashing red meat for you ScienceBlogs readers out there."

Dr. Bancel was pointed to my blog and felt I wasn't giving the full story. I'll give his comments and then at the end add some thoughts of my own. Bancel wrote:

]]> I find it disappointing that a Columbia faculty member should, in his public blog, be content to substitute facile derision for informed argument in criticizing a research article. It is an unfortunate choice, as it merely adds to today's wearisome environment of ad hominem public discourse, while missing an opportunity to educate.

I won't bother to explain here the errors in your post. Such explanations are all in the article - you would only need to spend more than "a few minutes" to appreciate that. There we explain why the RNGs are shielded, and we emphasize that the effect size is very small, which is essential to understanding why the experiment is run and analyzed the way it is. We do verify our results (as you suggest) with a re-sampling analysis over the full database of 4,000 days. All of this, again, is detailed in the paper.

You say these issues are incidental to your main critique. But it is not clear just what your main objection is. You indicate that the article is "very professional", but flawed, because we propose no theoretical framework (my interpretation of your second paragraph). This might be the entry point for an interesting discussion. But then - after tangential remarks - you pick this up at the end by suggesting (if I correctly read past the polemics) that we blindly manipulate our data, which is grossly wrong, and inconsistent with your opening comments.

It is regrettable that you have used a public forum to misrepresent work which you have, as you state, spent but a few minutes reviewing. It is also unfortunate if you have passed these misrepresentations on to a journalist. In your American Scientist article this summer, you warn journalists not to be misled by brash statements and to seek the best advice of scientists when writing about science. That works only if the scientists go the whole nine yards and make the honest effort to give good advice.

Lastly, I would say that I am doubly disappointed in your post since your own expertise is complementary to our own, and we benefit from any valid criticism based on a careful reading of our paper. Without hesitation, I'd say we welcome it.

I replied:

Thanks for the response. My blog represented my opinion based on a quick look, but I agree this is not my area of expertise. I would like to run your response (without comment from me) on both of my blogs. Would that be ok with you? I would like the readers to get both sides of the story.

To which Bancel replied:

If you feel my personal email to you is appropriate to post, please do so, but a brief response of explanation might be more interesting.
Perhaps you could suggest a couple of issues that I could address as it is still not clear to me just what your objections are.

I did appreciate two points you indicate in your post.

One is that you distinguish between the analysis and the topic itself. Most researchers conflate the admittedly questionable GCP hypothesis and the quality of analysis. These are, of course, separate issues.

The other is the difference in style between the social sciences and physics. This leads to unnecessary misunderstandings. I benefit enormously from interacting with scientists in different disciplines but the challenge is always to understand the mindset, since it determines how people frame the questions they ask.

As far as experimental physics (and the hard experimental sciences in general) and statistics, there are really 3 worlds here: laboratory research, where one works hard to achieve huge effect sizes. In this world one usually doesn't need to have much statistical sophistication. The second is modeling and simulation which is highly coupled to theory. The last is the experimental study of "natural records". This includes astronomy, geology, climate science, etc. Here you often take what you get and data can be noisy, heteroscedastic, etc. so that statistical sophistication is key. This is a caricature and of course these all overlap and interact. My point is that physics obviously isn't a monolith and good physicists may need some skills and not others. Presumably their training allows them acquire new skills as needed, often with the helpful guidance of colleagues in other fields.

I don't think it's appropriate for me to give long reply in response, so I'll just make a couple of general comments.

1. I think the biggest issue is that ESP is something that Bancel and Nelson are particularly interested in, but it's not something that I care about much at all. I don't want to go around claiming that ESP isn't real, or anything like that--I think it's enough to say that whatever effects are there, are very small, so small that they don't particularly interest me.

In contrast, I get much more irritated when people do bad science on topics that are potentially important (for example, the crappy studies I've mentioned on the blog on occasion, on topics such as political effects of the number of cabinet ministers in a country, or the alleged irrationality of voting, or the purported liberal voting tendencies of rich people, or, hmmm, was there something once about engineers having beautiful babies, or something like that . . . I can't quite remember . . .). Some statisticians get particularly outraged about shaky medical claims, but I don't know enough about medicine to get involved in such fights.

2. ESP statistics is pretty sophisticated. When you have large effects, you don't necessarily need sophisticated methods. But when effects are very weak, you might need very large sample sizes, sophisticated corrections for nonsampling errors, multiple comparisons adjustments, and so forth. I respect the statistical methods that have been developed in ESP research (and in psychometrics more generally), but I think they're still in a tough spot because of the small magnitudes of the effects they're studying.

As I've always said, what makes a statistician look good is not teasing out a small effect, but finding a huge effect that hasn't been noticed before. Sometimes fancy methods can help us find big effects (as in Red State, Blue State), but then we should be able to go back to the raw data and find these as well (again, as in Red State, Blue State). In that sense, the fancy methods are helping us do a more effective job of exploratory data analysis.

I don't have anything more to say about the Bancel and Nelson article in particular. It's out there, and youall can make your own judgments of it. (Please be polite in any comments. I appreciate that Bancel responded to my blog, and I don't want to reward him with a bunch of rude replies. Thanks.)

Notes from someone who's seen exactly 3 movies in the past 6 years

2009-11-16T07:56:49Z

1. From what I read, 2012 is a big-budget, low-brains remake of Miracle Mile, while completely missing the point of the original. So sad.

2. Meryl Streep was totally wasted in Fantastic Mr. Fox. And I don't mean she was drunk--well, maybe she was, who knows?--but her talent went largely unused. Seems like a crime to have Meryl Streep in a movie and not make more use of what she can do.

On the other hand, everyone deserves to relax now and then. If Streep is going to be taking a break, there's no harm in her doing it in the context of a movie.

And, on the plus side, they didn't let Gilbert Gottfried or anyone who sounds like him get anywhere near the place.

Email update

2009-11-15T21:58:27Z

Somebody in Nigeria wants to send me money. I can't give you the details, but let me say that if this does work out, I'll never have to worry about book royalties again. I feel a little guilty about dealing in blood diamonds, but if this deal works out, I can make it all right by donating a lot to charity.

"It would be as if any discussion of intercontinental navigation required a preliminary discussion of why the evidence shows that the earth is not flat"

2009-11-15T20:41:44Z

I've been ranting lately about how I don't like the term "risk aversion," and I was thinking it might help to bring up this post from last year:

]]> This discussion from Keynes (from Robert Skidelsky, linked from Steve Hsu) reminds me of a frustrating conversation I've sometimes had with economists regarding the concept of "risk aversion."

Risk aversion means many things, but in particular it is associated with attiitudes such as preferring a certain $30 to a 50/50 chance of having either $20 or $40. The standard model for this set of attitudes is to assume a nonlinear function for money. It is well known that reasonable nonlinear utility functions do not explain this sort of $20/30/40 attitude (see section 5 of this little article, for example); nonetheless the curving utility function always comes up in discussion, requiring me to waste a few minutes before going on, explaining why it doesn't explain the phenomenon.

It would be as if any discussion of intercontinental navigation required a preliminary discussion of why the evidence shows that the earth is not flat. . . .

Tobler's Law, Urbanization, and Electoral Bias: Why Compact, Contiguous Districts are Bad for the Democrats

2009-11-15T10:35:26Z

Jonathan Rodden and Jowei Chen sent me this article:

When one of the major parties in the United States wins a substantially larger share of the seats than its vote share would seem to warrant, the conventional explanation lies in manipulation of maps by the party that controls the redistricting process. Yet this paper uses a unique data set from Florida to demonstrate a common mechanism through which substantial partisan bias can emerge purely from residential patterns. When partisan preferences are spatially dependent and partisanship is highly correlated with population density, any districting scheme that generates relatively compact, contiguous districts will tend to produce bias against the urban party. In order to demonstrate this empirically, we apply automated districting algorithms driven solely by compactness and contiguity parameters, building winner-take-all districts out of the precinct-level results of the tied Florida presidential election of 2000. The simulation results demonstrate that with 50 percent of the votes statewide, the Republicans can expect to win around 59 percent of the seats without any "intentional" gerrymandering. This is because urban districts tend to be homogeneous and Democratic while suburban and rural districts tend to be moderately Republican. Thus in Florida and other states where Democrats are highly concentrated in cities, the seemingly apolitical practice of requiring compact, contiguous districts will produce systematic pro-Republican electoral bias.

My thoughts:

]]> This is cool stuff. Lots of people (going back at least to Bob Erikson in 1972) have talked about the idea that the geographic distribution of voters in modern times favors the Republican Party. The idea is that Democrats are concentrated in high-density areas, and thus geographically-compact districting plans will tend to pack Democratic voters into districts where they have 80% of the vote or whatever, thus wasting their votes. But the present article goes further than previous speculation and even previous data analysis by working with the (nearly) exact location of the voters.

The analyses in the article are great, and it's fun to see how they play around with the spatial data. A lot more can be done here, I'm sure.

But I'm confused by one thing they write: "we take a unique empirical approach to the analysis of electoral bias. Rather than using district-level information to simulate hypothetical tied elections, we use precinct-level data from an election that was almost an exact tie." It seems to me they're mixing two ideas here:
(1) Using precinct-level rather than district-level data.
(2) Using a tied election rather than taking an election that's, say, 53-47 and shifting it by 3 percentage points.

For point (1), yes, of course precinct level data are better, and it's great that they put in the effort to get such data. Presumably earlier researchers would've used precinct-level data too, had such data been readily available.

For point (2), sure, if you happen to have a tied election, fine. But if you want to extend inference to non-tied elections, then you gotta to what you gotta do. You can't just keep going back to Florida in 2000 or Missouri in 2008 or whatever, over and over again.

Anyway, I'm not saying they're doing something wrong here, it just seems funny how they're presenting the strengths and limitations of their method. I didn't read every word of the article, but I assume they could apply their ideas to non-tied elections just by shifting to 50/50. And, as Gary and I discussed in our 1994 articles, even if you don't introduce any national swing at all, you still might want to include variability in your hypothetical replicated elections.

The punchline:

In contemporary Florida, partisans are arranged in geographic space in such a way that virtually any districting scheme favoring contiguity and compactness will generate substantial electoral bias in favor of the Republican Party. This result is driven largely by the partisan asymmetry in voters' residential patterns: Since the realignment of the party system, Democrats have tended to live in dense, homogeneous neighborhoods that aggregate into landslide Democratic districts, while Republicans live in more sparsely populated neighborhoods that aggregate into geographically larger and more politically heterogeneous districts. This phenomenon appears to substantially explain the pro-Republican bias observed in Florida's recent legislative elections.

More fundamentally, I guess this might be considered a pro-rural or pro-suburban bias, or an anti-urban bias which would fundamentally alter the representation of different parts of the state, no matter which parties happen to represent them.

One thing that surprised me is that Chen and Rodden did not suggest multimember districts as a way to balance the playing field. Is this a proposal that Democrats in Florida (or elsewhere) should be making?

One other question. If more Democrats tend to win in super-safe districts where they get 70% or 80% of the vote, does this imply that they will be more free in their voting patterns to indulge their personal preferences, compared to Republicans who (on average) might be under more electoral pressure and have to worry more about reelection?

Other things

The graphs are just beautiful. They clearly had fun working with these data.

A few minor comments:

- Table 1 is just silly. "[0.0141, 0.0145]"? Excuse me? "+0.219778"??? You gotta be kidding me here.

- Figures 1 and 2 are fine, but the kernel density in the corner is just tacky. A histogram is the way to go here: it's better to just see the data directly.

- I have no problem with Figure 3, except that they shouldn't use the red/blue color scheme--that's highly confusing given that the colors meant something different in the other figures.

- Figure 4: I'm not really happy with a "local spatial autocorrelation index" that has numbers like 1000 and 2000. Perhaps you can give it a different name; we're all trained to thing of "correlations" as going between +1 and -1. Also, with these colors, I think you'd get some improvement if you added purple for the close precincts. Otherwise you're getting some noise from the essentially arbitrary colorings of the precincts that are near 50%.

- Figure 5: The y-axis goes below 0 and above 1. That's a no-no when displaying proportions. Also, make the dots slightly smaller (I know you can do it; see Figure 1); the overlappage is a bit distracting.

- Figure 6: Cute.

- Figure 7. Something's wrong with your histogram. On the label it says 1000 simulations, but the y-axis goes up to 600. If the highest histogram bar has 600 points, then the total histogram has many many thousands! Better, I think, to just remove the y-axis entirely.

- Figure 8. A bit confusing to have square graphs with axes on different scales. Just make x and y axes both go from 0 to 1.

- Figure 9: Hey, you used JudgeIt! Cool. Also, please label the lines directly on the graph, and give them different colors! Don't use that ugly legend that forces the reader to go back and forth, back and forth, to read the damn graph. Also, can't you go back earlier than 1992?