I’m introducing a new feature this weekend I’m calling “Blogging the Journals”, in which I take one article from a major journal in my field (American Political Science Review, American Journal of Political Science, Public Opinion Quarterly, Asia Survey, and The Journal of East Asian Studies) and dissect it- looking for references missed, theoretical considerations overlooked, methodological innovations, big time findings, and misarticulated results. Or perhaps to give the brilliant authors a big, wet, sloppy scholarly kiss for their groundbreaking contributions to the field. After the jump, I turn to the first article in APSR’s February edition, “Cycles in American National Electoral Politics, 1854–2006: Statistical Evidence and an Explanatory Model” by Merrill, Grofman, and Brunell.
I’ve got to admit upfront- I’m skeptical of the validity of Political Cycle studies, and even more skeptical of their utility. Full citation and close reading after the jump.
Merrill, Grofman, and Brunell, “Cycles in American National Electoral Politics, 1854–2006: Statistical Evidence and an Explanatory Model”. American Political Science Review (2008), 102: 1-17 Cambridge University Press. doi:10.1017/S0003055408080064, Published online by Cambridge University Press 13Feb200.
As I mentioned above, I am deeply skeptical of political cycle studies, if for no other reason than it is very difficult to come to a consensus about what a political cycle is. Some scholars think is is waves of partisanship or ideology in public opinion (or mood, as in The Macro Polity), some think it is partisan control of institutions (which institutions, though? the Legislature, Presidency? what happens in the case of divided government? where is the cycle then?), some think that it is a demographic reorganization of the parties’ constituencies (actually, this is called realignment and I depart from these authors in calling realignment a very different idea than political cycles), so call it a redefinition of the salient political issues (again, I must depart from the authors, as a new set of salient issues is rarely cyclical).
So a cycle must therefor be a shift in public mood from conservative to liberal and back again, a shift from public support for party A to party B and back again, or a shift from one party’s control of the institutions of power to another and back again. The authors of this piece choose the least interesting alternative, in my opinion, and attempt to explain cycles of party control of institutions.
Unfortunately, this is a bit like the “ah-ha!” moment of discovering that indeed, the sky is blue (not just rumors all these years). Political cycles are mostly unavoidable in any two party system (see Gary Cox’s excellent body of formal theory work to show why American institutions nearly guarantee a stable, long term 2-party dominated system), as by definition for government to change hands, it must go from the hands of one party to another and back again. It seems to me there is very little left to explain about political cycles once one understands that a two party system will alternate between two parties. If we are to make the heroic assumption the democracy is not completely misplaced and assume that at least some of the electorate is not voting randomly and that those votes have the potential to change the outcome of elections, then we must also assume that the shifts in party power are not random- not that they are determined by anything particular, just that they are not random. I find that a rather uncontroversial claim, and any reader of empirical political science or public opinion in the last 50 years would agree (even Phillip Converse). The authors of this piece still believe that the non-randomness of party control, despite overwhelming political science to the contrary, needs to be proved. that in part, demonstrates what is so wrong with this article and what is so wrong with the APSR in particular. As the flagship journal in the field, it should focus more on good scholarship than sexy methods, and unfortunately, sexy methods are about all this piece has to offer.
This first two-thirds of this article are a perfect case of bad statistics posing as good science. Throughout, the authors set up null hypothesis straw men that their tests conveniently disconfirm. The authors lead off with what they consider an argument for the utility of this type of study, a series of predictions made by Arthur Schlesinger, Sr.:
For example, Arthur Schlesinger, Jr. (1986) reports his father’s famous prediction in a 1924 lecture that “Coolidge-style conservatism would last till about 1932,” his further prediction (Schlesinger 1939) that the “prevailing liberal mood would run its course in about 1947,” and later in 1949 that the “recession from liberalism was due to end in 1962,” and that the “next conservative epoch will commence around 1978.” That these predictions of mood changes about every 15 years were on target not only reflects the elder Schlesinger’s understanding of history but also suggests that somewhat regular cycling of political dominance may occur, or as his son puts it, “Predictive success creates a presumption in favor of a hypothesis” (Schlesinger 1986).
I don’t mean to be flip here, but if Professor Schlessinger could predict all of this without complex statistical analysis or a new complex model, what use is this study? But I digress. The authors go on to point out the great debates among great scholars about the cyclical nature of American politics. They decide on measuring cycles not as Dr. Schlesinger does, as ideological swings, but using the more easily available metric of vote (for president) or seat (for Congress) share by party. Their first test of the idea of the cycles is a simple one (both definitions of simple apply). They test the election data from 1854-1980 for runs (periods of uninterrupted partisan dominance in the House/Senate/White House, which may be a short as one election cycle or as long as any party can hold on). They test the data for runs against the null hypothesis that partisan control is random and completely unrelated- a null hypothesis that is staggeringly dumb, but that a few of my professors from my early graduate career would have accepted as a good null. Fluctuations in party control are not random. We know that. Any Bayesian will tell you. Assuming that partisan dominance over either house of congress is random is like assuming that the Earth is flat and then proving otherwise. There’s really no need to “establish” it here and it adds nothing to their forthcoming analysis, which thankfully, gets better.
The second third of the paper is taken up by applying spectral analysis to the analyze the democratic seat/vote share over time. This is how the authors explain it:
In order to investigate the possibility of cycles in historical time series, we perform a spectral analysis—–a procedure that decomposes the pattern over time into a spectrum of cycles of different lengths, just as a prism decomposes white light into a spectrum of colors of different wavelengths or frequencies (Bloomfield 2000).
In other words, they use statistical devices that make them seem smart and innovative to do something that I could do with notepad and show with a line graph. Actually, I did. I took their data available on their website and got the same results. I suppose what the spectral analysis is supposed to add here is proving that the fluctuations of party control/vote percentage are not random and in fact have a semi-regular frequency. I see what they’ve done, but I’m not sure I bite. There is too much noise in the data. If the thing we are out to prove is the existence not just of alternation but of regular or semi-regular cycles that are useful in understanding American politics in their own right, I need some compelling reason to dismiss the outliers, or at least a good reason why there are so many exceptions to the cycle. So far we haven’t proved that there are cycles, but rather proved that the change in party control is not random and that parties tend to hold on to power longer than a couple of rounds or elections.
Their spectral analysis shows that the average time between one party’s assumption of power and the time they resume power having lost it in the interim comes out to be about 26 years. The spectral analysis is the part tells us that the average cycle is the most frequently observed cycle. So now we have dependent cycles in semi-regular intervals- something like political cycles that Schlesinger, Sr. saw without the aid of fancy statistics. They then conclude that since the average cycle length is 26 years, the average time in power for a party must be 13. This is a bit of a leap without explanation.
The whole of the article up until this point has not told us anything more useful or more simple than we have known before, and has needlessly complicated the points leading up to their central argument.
The third part of the article (and really the only interesting part) is the attempt to model these party dominance cycles. Their theoretical model contains four elements that have (potentially) contradictory pulls, setting in place an (essentially) two dimensional model:
α = median convergence parameter vs. β = party policy-motivation parameter
γ = in-party advantage parameter vs. δ = voter reaction parameter
in this case, α and β pull in opposing directions (almost by definition we assume the the median voter is less extreme that the policy-oriented party preference, therefore, parties face contradictory pressures to conform to the median voter and their own policy references) and γ and δ pull in opposing directions because the incumbency advantage (γ) is mediated by negative voter reaction to incumbency (δ), as described in the article. They explain that party medians and voter medians are dynamic and that the negative feedback loop created by the above parameters is the cause of the semi-regular cycles in American Politics. The model is well thought out, however, I fail to see why a model that complex helps explain a phenomenon as simple as political cycling in a two party system. The major problem with their model comes not from the theory but how they test it.
I’ll say it again, the theory is really nice. The test, however, is a load of hooey. Rather than find good data to serve as proxies for these parameters, they estimate model parameters not using actual data, but rather but an iterative method that finds the parameter values with the best fit for the dependent variable. Let me put that in plain English. They had a computer keep guessing at parameter values until it made the model fit the data. I understand that some of the data they would need to test the theory would be hard to collect and controversial, but how much can we learn from a theory whose utility is proven is this way? There is no predictive capability to their model if we can’t plug in actual data and get decently accurate outcomes. If i wanted to make a prediction based on this data for the outcome of the 2008 elections, I would have no estimate of the parameters other than the constants provided (which, if you look hard at the graphs below, they show that there will never again be less than a majority of Democrats in the House (hip-hip!) or in the Senate (hoorah!). Yes, that’s right. according to this model, the Democrats will own the house forever and ever, amen. That’s what happens when you strip context from analysis and estimate parameters based on outcomes rather than based on measurements. As conforting as it might be to picture a congress of democrats forever, I’m not getting my hopes up, and a strongly doubt that the DNC is going to take any consolation.
I have a lot of problems with this article, but the biggest problem is the lack of actual data. The only data used in this article, the only data, are the data on vote/seat share. Despite their interesting theory, the collect no data on public opinion (though it is available for at least part of their time period- the SNES or The Macro Politiy come to mind) they make no effort to estimate party medians (NOMINATE? DNOMINATE?). The test of their model is how well if fits the data after they have smoothed the data and their model predictions and fit the model to the data. The proof of the theory is wholly dependent on the dependent variable. This is not good science, no proof of the model, and a shame for the APSR.
In the end, this article, like many in the APSR, winds up being about methods rather than the subject and content, which here is surprisingly empty for a flagship journal. I’m not sure what this adds to our collective knowledge beyond The Macro Polity and Downes and Alesina and Rosenthal other than to attempt to put a fine point on political cycles by an untested if well thought out theory, which, because they are subject to fluctuations and events, neither needs nor can sustain such a fine point. The authors’ primary theoretical strength borrows from Erikson, Stimson, and MacKuen. While it’s interesting to plug it into a new methodology, it doesn’t reveal anything more than how clever the modelers are. In essence, the electoral connection is sustained as the public mood shifts in “a negative feedback loop” (their term) against incumbents as incumbents face political first political success then stalemate as issues are resolved or shelved. This must be expected in a two-party system that remains uncaptured by a single dominant party. I’d really like to see political cycle analysis, though not this one, done on a country like Japan to see if policy, public mood, or seat share (if not majorities) switch systematically over time in response to government actions in cyclical ways.
Comments? Suggestions for next week?
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