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Party mandate theory and time-series analysis: a methodological comment
Electoral Studies 18 (1999) 569–585 www.elsevier.com/locate/electstud
Party mandate theory and time-series analysis: a methodological comment Helmut Thome* Institut fu¨r Soziologie, Martin-Luther-Universita¨t Halle-Wittenberg, D-06099 Halle (Saale), Germany
Abstract In 1990 Ian Budge and Richard Hofferbert published an article in support of “the doctrine of the party mandate”, using evidence from regression analyses relating the content of postwar US party platforms and governmental outputs in terms of yearly expenditure rates. Their approach was severely criticized by Gary King and Michael Laver (1993) but has been maintained by the authors in a subsequent extension of their analysis to include data from Australia, Canada and seven European States. The present article takes issue with both the approach followed by Budge and Hofferbert and the alternative approach recommended by King and Laver. It is argued that the trend problem has not been adequately dealt with and the formalization of the mandate model lacks conceptual consistency. Three major suggestions emerge from the discussion: (1) the formal mandate model should be extended to include a “divergence term” designed to separate positive from negative mandate effects; (2) the analysis should pay closer attention to the parameter restrictions that follow from the theoretical model; and (3) the regression equations should be interpreted heuristically in terms of “cointegration” or “causal-trends” models. 1999 Elsevier Science Ltd. All rights reserved. Keywords: Party mandate theory; Cointegration models
1. Introduction In 1990 Ian Budge and Richard Hofferbert published an article in support of “the doctrine of the party mandate, according to which the competing parties offer to the voters different governmental programs between which they can choose. The party * Tel.: ⫹ 49-0345-5524260; fax: ⫹ 49-0345-5527149; e-mail: [email protected] 0261-3794/99/$ - see front matter 1999 Elsevier Science Ltd. All rights reserved. PII: S 0 2 6 1 - 3 7 9 4 ( 9 9 ) 0 0 0 1 5 - 3
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which attracts the most votes on this basis then forms the next government, but it is bound…to carry through the program on which it has been elected” (Budge and Hofferbert, 1990, p. 111). By way of regression analyses, they established what they thought to be “strong links” between postwar (1948–1983) election platforms (coded into 54 subject categories indicating programmatic emphases across several issue areas) and governmental outputs (in terms of yearly expenditure shares) in the United States. The methodology Budge and Hofferbert had followed was strongly criticized by Gary King and Michael Laver (1993) who, in their reanalysis of the data, concluded that “party platforms have small or nonexistent effects on government spending”. In their reply to King and Laver’s critique, Hofferbert et al. (1993) defended their original thesis and methodology, arguing that level relationships must be maintained and that “mandates” only involve an “association, not necessarily a causal connection”, between party programs and government policy. This position was also upheld in a book that extended their previous analyses to include data from Australia, Canada and seven European States (Klingemann et al., 1994). In a review of this book it was noted that “[it] is heavy on method and data… It serves as a quiet but powerful reminder of the power of evidence” (Stevenson, 1995, p. 186). Thus it might be appropriate to reconsider the methodological arguments presented by King and Laver versus those presented by Hofferbert and his colleagues, especially since their debate raises more general problems typically involved in time-series analyses of social data. In Section 2, I discuss the “general program model” proposed by Budge and Hofferbert (henceforth called the “B-H model”)1 and suggest an extension of the formal model which should make for a more adequate representation of the theoretical concept. In Section 3 it is argued that the partial adjustment model introduced by King and Laver (1993) does not adequately solve the trend problem which motivated its construction. In Section 4 I argue that Budge and Hofferbert are right in deriving from their theoretical model long-run co-movements between the trending content of party platforms and trending governmental output. These co-movements, however, cannot be simply presupposed but must be demonstrated empirically. I suggest to apply, at least heuristically, “cointegration” or “causal-trends” models, to this task. Concluding remarks follow in Section 5.
2. The Budge–Hofferbert mandate model Like King and Laver I shall focus on the US data and “Model 5”, the mandate model, which “is the one that corresponds most closely to the idealized mandate theory” (Budge and Hofferbert, 1990, p. 120). It is given here in Eq. (1) with minor notational changes: E(Yt ⫹ 2) ⫽ ␣ ⫹ dDt ⫹ rRt ⫹ pdDt·Gt ⫹ prRt(1 ⫺ Gt).
(1)
1 In the original paper the model is also referred to as “model 5”. In the book (Klingemann et al., 1994, pp. 48–51) the same model is called the “agenda plus mandate model” and shortened to “mandate model”.
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Greek letters are parameters to be estimated. Yt+2 represents the percentage of the total US government budget devoted to a specific policy area, like “Education & Employment Services”, in a certain year t ⫹ 2. Dt represents the percentage, two years earlier, of the Democratic party platform that was devoted to a policy area matched to the spending category; Rt refers to the percentage weight of the same policy area in the Republican platform; Gt is a dummy variable which takes on the value of “1” in the years of a Democratic president and “0” in the years of a Republican president. (The variable (1 ⫺ G) thus takes on the value of “0” in the years of a Democratic president and “1” in the years of Republican presidents.) The multiplicative terms have been included to allow for the (hypothesized) possibility that a party’s influence on the federal budget varies depending on whether or not the party holds the presidency. The core assumption of mandate theory is that the winning party, more so than the losing party, should be able (and willing) to pursue policy preferences in accordance with its own party platform. Since party platforms only change every four years the platform variables are recorded as intermittent step changes; four successive years, for example 1952 through 1955, are all given the same value decided upon at the 1952 convention. The estimated parameters therefore indicate the average effect of a percentage shift of a certain platform category over a four-year period under the assumptions (1) that the effect materializes not before the second year following the last party convention, (2) that it extends two years into the next presidential term and (3) that there is an interactive effect linking party platform and presidential office. To give an example, we look at the estimation results for “Education & Employment Services” (see Table 3 in Budge and Hofferbert, 1990, p. 122), which is the regression equation with the highest coefficient of determination (R2 ⫽ 0.88): ˆ d ⫽ 0.66, ˆ r ⫽ ⫺ 0.12, ˆ pd ⫽ 0.55, ˆ pr ⫽ 0.50 where d and r, the main effects, are called “agenda effects” by Klingemann et al. (1994), whereas the multiplicative effects, pd and pr, are called “(pure) mandate effects”; the sum of the party effects—(d ⫹ pd) or (r ⫹ pr)—will be referred to as “total effects” of the party in office. If we accept the model and its parameters as they stand now, the interpretation is as follows. If the Democrats increased (lowered) their platform emphasis on education and the Democratic candidate won the subsequent presidential election, then spending-shares on education increased (decreased) by (0.66% ⫹ 0.55%) ⫽ 1.2% per unit change in the amount of platform content devoted to education. If the losing Republicans had, at the same time, lowered their platform emphasis on education, this would have further increased the expenditure share of education due to the negative weight of ˆ r ⫽ ⫺ 0.12. Klingemann et al. (1994, p. 50 ff.) call this a “negative mandate” effect. It also follows from the estimated parameters that the Democrats, if not in office, still manage (contrary to the Republicans) to move government expenditures on education in the direction of their own programmatic emphasis. For the losing party the multiplicative term is zero. If the Republican Party wins the presidential election, then, according to this model, it will push the spending-share on education with the weight of ˆ r ⫹ ˆ pr ⫽ ( ⫺ 0.12 ⫹ 0.50) ⫽ 0.38 in the direction of its own platform emphasis,
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but the Democrats can outweigh this move with their main effect coefficient of ˆ d ⫽ 0.66 if their programmatic emphasis has changed in the opposite direction. To sum up, d and r give the total effect of the respective “out-party”, ˆ pd and pr “tells us the difference in the translation of program to policy of Party A’s program when that party wins, relative to when it loses” (Klingemann et al., 1994, p. 50). The first point of controversy has been phrased in terms of significance testing, but what really is at issue here are the restrictions that the theoretical hypotheses place upon the model parameters. King and Laver (1993) infer—correctly, I think— from the theory outlined in Budge and Hofferbert (1990) that the total effect for both parties should be positive: (d ⫹ pd) > 0 and (r ⫹ pr) > 0. Consequently, it is not sufficient to test the conditional significance of the main and the interactive effects singly; one needs to estimate the standard error of the total effect (which Budge and Hofferbert, 1990, had not provided). When King and Laver performed adequate tests, they found that only 10 out of 24 total effects (for two parties and 12 spending categories) were significant on the 5% level. One might argue about the appropriate level of significance; but note from Table 1 in King and Laver (1993, p. 747) that 10 of the estimated sums (total effects) are even negative and two of the positive ones are less than 1.2 times larger than their respective standard errors, a third one is only 1.45 times the size of its standard error. Thus, even if we lower the required significance level quite a bit and apply a one-sided test, the model fails in at least half the cases. The actual disconfirmation, however, is even stronger if one takes into account that the model applies to both parties at once and that, for each equation, the restriction should hold that (d ⫹ pd) > 0 and (r ⫹ pr) > 0. This requirement is met by only two of the 12 policy areas for which the B-H model has been tested on US data. Hofferbert and his colleagues apparently want to focus on the interactive effects, pd and pr; i.e., on the “difference in the translation rate of the Republican and Democratic platform, respectively, when that particular party wins relative to when it loses”. They find “in 13 of the 24 instances reanalyzed by King and Laver, winning matters for positive translations of a party’s platform emphases into expenditure priorities. This, we think, is important” (Hofferbert et al., 1993, p. 748). Yet this distribution hardly supports the model; one would expect such a result from a random experiment in which positive and negative outcomes have equal probabilities. Finally, Hofferbert et al. (1993, p. 748) argue: “Second, and more important, one must recognize that a positive coefficient for the winning party’s favoured policy does not necessarily mean that the net spending share increases when the party takes office”. This observation does not affect King and Laver’s argument at all. The expected net change in expenditure share, Yt ⫺ Yt−1, could even be negative if all the coefficients were positive and the winning party had increased its platform emphasis on Y—it could still be negative if the losing party had decreased its platform emphasis to an extent that would outweigh the increased emphasis of the winning party. In their original paper, Budge and Hofferbert explicitly (but erroneously, I think) made the restriction that the main effect coefficients should be negative (Budge and Hofferbert, 1990, p. 119). Later, in the book, this restriction was lifted and negative main effects were interpreted to constitute a special case called “nega-
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tive mandate”. What the authors mean by this is stated in the following way: “Incumbents may have a mandate not only for their own particular programmatic emphases but also against specific other favourite themes of the losers. If Party A’s program stresses welfare and Party B’s stresses defence, when Party A wins, its mandate could be read as both a call for increased welfare and also for decreased defence, on the grounds that the voters’ preferences in voting for Party A may have been either positive (pro welfare) or negative (anti defence). The vote can convey a positive and/or a negative mandate… In the case of the positive mandate, the multiplicative terms (1 ⫻ the program percent for Party n’s emphasis on topic i when in government; 0 when out)—b(Pni ⫻ G)—will have a positive sign (+). In the case of the negative mandate, the simple term—bPni—will have a negative sign (−)” (Klingemann et al., 1994, p. 50 ff.). Note that, according to the second part of this definition, the sign of the main effect of Party A indicates the negative mandate of Party A, and not that of some other Party B. Though the concept of the negative mandate is substantively clear, its operationalization in terms of a negative main effect coefficient is unsatisfactory; it even contradicts the underlying theoretical concept. First, the operational definition is incomplete. If, for some Party A, the main effect is negative and the multiplicative effect is positive, does this mean that A has a negative and a positive mandate? Second, if the negative mandate of the winning Party A arises in reaction to the losing Party B’s opposite shift of policy emphasis (or de-emphasis), how can it be made a function of A’s own platform emphasis as the definition just quoted has it? The answer is, it cannot. In their actual analysis of the US data (now covering the period from 1948 to 1990) Klingemann et al. (1994) use another definition by treating the negative main effect of the losing Party B as being indicative of the negative mandate of the winning Party A. This seems to make sense as long as the winning party and the losing party shift their platform emphasis in opposite directions. Consider again the previously presented example of “Education & Employment” and suppose that the Democratic candidate wins the election, after his party’s platform increased its emphasis on education and the Republicans decreased theirs. In such an instance, one has to expect (from the estimated model given above) a positive shift in the expenditure share of education due to the positive total effect of the Democratic platform shift and an added positive effect resulting from the negative change in Republican emphasis on education weighted by the negative main effect coefficient r. The Republican party, however, is not always the loser; and the model must equally apply to both parties’ winning or losing, increasing or decreasing their emphasis. What can be predicted from the same estimated model, if, for example, the Republicans win the election after de-emphasizing education contrary to what the Democrats do in their platform? Since the main effect estimate is negative, ˆ r ⫽ ⫺ 0.12, de-emphasizing produces a positive change component which must be out-weighted by a positive interactive effect ˆ pr > 0.12 multiplied by a negative change. We again encounter the restriction that the total effect should be positive for both parties, if the mandate model is correct. But now consider a pre-election situation where both parties, the Democrats and the Republicans, increased their emphasis on education. Then a newly installed Democratic
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administration would, according to the model, increase its spending on education less than in the previous situation where the Republican platform moved in the opposite direction. That is, the “negative mandate” of the governing party (as long as it is defined by the negative main effect of the losing party’s platform) implies the expectation that the winning party always acts less in accord with its own party platform if it has the support of the losing party than it would be the case if the losing party’s platform had been changed in the opposite direction. This may indeed happen under special circumstances; but for the general model (which does not specify these circumstances) this implication runs counter to mandate theory. Thus, the restriction must be maintained that neither the main (agenda) nor the multiplicative (mandate) effect should be negative. The concept of a negative mandate has to be operationalized in a different way. One solution to the problem might be the addition of two higher-order multiplicative terms that further specify the effects of incumbency for both parties according to whether or not the winning party’s most recent platform change diverges from (or is congruent with) the most recent change of emphasis in the losing party’s platform. Technically speaking, the multiplicative term D·G in Eq. (1) needs to be multiplied by a second dummy variable, say “NM” (Negative Mandate) which has, in four consecutive years, the value of “1” if in an election year the Democratic and the Republican platform emphases have shifted in opposite direction; if the emphasis shifts of the two parties do not diverge, NM is “0”. Likewise, the multiplicative term R(1 ⫺ G) representing the effect of the Republican presidency needs to be multiplied by the same dummy variable NM. The expanded model is given by Eq. (2): E(Yt ⫹ 2) ⫽ ␣ ⫹ dDt· ⫹ rRt ⫹ pdDt·Gt ⫹ prRt(1 ⫺ G)t
(2)
⫹ dnm(D·G·NM)t ⫹ frm[R(1 ⫺ G)NM]t. The restriction that the parameters r, d, pd and pr should all be positive still applies. The expanded model clearly ties the concept of a “negative mandate” to the occurrence of divergent party platforms (in the sense explained above). Whereas a positive mandate is represented by pd (for the winning Democratic president) or pr (for the winning Republican president), a negative mandate is indicated by dnm > 0 (for the Democratic president) or by dnm > 0 (for the Republican president). Whether or not such positive divergence effects occur is a purely empirical question. The estimates may even be negative without contradicting mandate theory—if only the sum of all three coefficients remains positive for each party. A negative coefficient dnm or rnm tells us that the president’s power to pursue his own party’s programmatic preferences is lowered if the opposition party has shifted its emphasis into the opposite direction. The influence of the losing party’s platform emphasis is indicated by the (positive) main effect, if no “divergence” occurs. If the two platforms diverge, the negative mandate effect of the winning party (e.g., the Democrats) must be taken into account. The (possibly negative) influence of the “out-party” (e.g., the Republicans) is then given by the difference (r ⫺ dnm). Given the shortness of the time series available so far and the very few instances of diverging or converging platform changes between 1948 and 1983 (or even 1990),
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parameter estimation becomes rather hazardous. Nevertheless, an example will be presented at the end of Section 4, after additional problems of modeling and estimation have been discussed. 3. The partial adjustment model proposed by King and Laver King and Laver (1993) address yet another problem which often troubles the timeseries analyst: the presence of pronounced trend components. Budge and Hofferbert (1990) decided to ignore the clear secular trend exhibited in most of the budget figures they have analysed. The platform variables, too, are non-stationary. Trending data violate one of the core assumptions in ordinary least-squares estimation: that the observations are statistically independent from each other. As King and Laver rightly point out, “regressions with trending variables, very high R-squared values, and bad Durbin–Watson statistics are exactly the situation…described [as] ‘spurious regression’” (King and Laver, 1993, p. 745). In such a situation, the coefficient of determination tends to be largely inflated, the estimated standard errors of the regression coefficient are biased and significance tests become unreliable. Budge and Hofferbert (1990, p. 118) report that “various tests conducted on the effects of time as an influence both on emphases and expenditures demonstrate a limited effect that by no means detracts from the independent influence of platform emphases on spending shares”. This empirical result, however, does not indicate that trend has no relevant impact on estimation. If the trend is not deterministic but stochastic (which is rather likely with social and cultural indicators), the inclusion of a time variable into the regression equation makes little difference and does not remove spuriousness from estimation. For example, Nelson and Kang (1984) found out in their experimental studies that independently generated random-walk processes (that, by definition, are stochastic trends), if regressed on each other, produced an average coefficient of determination of R2 ⫽ 0.50. When a time variable was included, the correct null hypothesis of no relationship was still rejected in 64% of all cases, though the level of significance had been set at 5%. Without the inclusion of a time variable Banerjee et al. (1993, p. 74 cont.) established a rejection ratio of 75%. From these and other studies we learn that detrending a series by a polynomial function of time or, equivalently, by including a time variable among the regressors is not an effective control on spuriousness caused by the presence of stochastic trend components. Specific circumstances may be given where trending variables are not harmful: the case of cointegration. Since King and Laver do not discuss this possibility (although it is suggested by party mandate theory) I shall not consider it before Section 4. King and Laver (1993) try to circumvent the trend problem by proposing a new model which substantively differs from the B-H model and also seems to control effectively the impact of trend. They first accept the basic premise of the B-H model that the preferred expenditure share, YP, is a function of the relative amount of emphasis, X, that a certain policy area receives in the party platform:2 2 I give a more elaborate presentation of the model proposed by King and Laver in order to render my subsequent arguments more intelligible. For the following see almost any econometric textbook, e.g., Greene (1993, p. 526 cont.), Maddala (1992, p. 415 cont.) or Kmenta (1986, p. 528 cont.).
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YPt ⫽ ␣ ⫹ Xt ⫹ ⑀t, ⑀t 苲 i.i.d.(0,).
(3)
To simplify derivations, Eq. (3) (and the following ones as well) are written with one regressor variable only; the time lag is also excluded. Note that Eq. (3) states an equilibrium relationship, where  indicates how much change in the preferred spending level eventually arises from a unit change in a party’s platform emphasis. To this model King and Laver add the assumption that the change in the actual level of spending, Yt, does not come about at once (within one time interval) but unfolds gradually.3 More specifically, they assume that Yt is determined by a weighted average of the previous value, Yt−1, and the preferred level Yt ⫽ ␥Yt ⫺ 1 ⫹ (1 ⫺ ␥)YPt , where 0 ⱕ ␥ ⬍ 1
(4)
or, equivalently, (Yt ⫺ Yt ⫺ 1) ⫽ (1 ⫺ ␥)(YPt ⫺ Yt ⫺ 1).
(4a)
The coefficient (1 ⫺ ␥) is called the “adjustment coefficient” since it indicates the rate of adjustment of Yt to YPt . The larger it is the more rapidly Yt moves towards its equilibrium value YPt . Combining Eq. (4a) and (3) gives Yt ⫽ ␣(1 ⫺ ␥) ⫹ (1 ⫺ ␥)Xt ⫹ ␥Yt ⫺ 1 ⫹ (1 ⫺ ␥)⑀t,
(5)
which can be written as Yt ⫽ c ⫹ Xt ⫹ ␥Yt ⫺ 1 ⫹ ut,
(6)
with c ⫽ ␣(1 ⫺ ␥), ⫽ (1 ⫺ ␥) and ut ⫽ (1 ⫺ ␥)⑀t, where ut has the same properties as ⑀t in Eq. (3). From this it follows that the slope of the equilibrium relationship given in Eq. (3) can be retrieved by ˆ ⫽ ˆ /(1 ⫺ ␥ˆ ). It is called the “long-run impact” or “equilibrium” multiplier, whereas is referred to as the “immediate” impact multiplier. Note specifically that “Gamma”, the coefficient of the lagged endogenous variable, Y(t ⫺ 1), has part in it. Eq. (6) is the well-known geometric lag or first-order autoregressive distributed lag model which is open to several (and partly competing) substantive interpretations, the “partial adjustment model” being only one of them.4 King and Laver (1993, p. 746) set up the OLS estimation equation for their partial adjustment model in the following way (with minor notational changes) E(Yt) ⫽ *0 ⫹ *rRt ⫺ 2 ⫹ *dDt ⫺ 2 ⫹ *pd(D·G)t ⫺ 2 ⫹ *pr[D(1 ⫺ G)]t ⫺ 2
(7)
⫹ yYt ⫺ 1.
3 Remember that Budge and Hofferbert assumed a two-year delay before a new president could influence the budget. 4 Cf. Beck (1991) and King (1989, ch. 7). On the mathematical equivalence of substantively diverging models, also see Banerjee et al. (1993, p. 48 cont.).
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Eq. (7) differs from the B-H model in Eq. (1) merely by the added endogenous term Yt−1; it does not include the “divergence term” introduced in Section 2. If only one endogenous term with lag k ⫽ 1 appears on the right-hand side it has to “take care” equally of all the exogenous variables in the equation which, in this case, implies (1) the assumption of identical adjustment rates (equal speed, but not equal amounts) for the winning and the losing party in transferring their platform changes (positively or negatively) into changes of expenditure shares in the federal budget.5 With the platform levels fixed to the same value for four consecutive years and the given time lag of k ⫽ 2, the model also implies (2) that the impact of a platform change will gradually build up and reach its highest level two years after the end of the presidential term for which the platform had been set up. One wonders if these two assumptions approximate reality more closely than Budge and Hofferbert’s estimation of an average impact for the same four-year period. This is a substantive issue that I shall not discuss here. King and Laver claim that their model “eliminates…most of the problems with autocorrelation and nonstationarity” (King and Laver, 1993, p. 746). Their major concern is the statistical significance of the immediate impact multiplier. They report that only four of the 24 sums of estimated coefficients—(ˆ d ⫹ ˆ pd) and (ˆ r ⫹ ˆ pr)— turned out to be significant on the 5% level.6 The major problem with their approach is that the parameters of the partial adjustment model (just like those of any other dynamic model) cannot be adequately estimated and tested with non-stationary data (Kmenta, 1986, p. 531)—unless the processes are “co-integrated” (see Section 4 below) and the partial adjustment model becomes the “error correction” part in a more comprehensive model (Engle and Granger, 1987; Maddala, 1992, p. 420; Beck, 1991). Consider again the coefficient of the lagged endogenous variable: it is “overburdened” with representing (and confusing) three types of effects originating from (1) the trend in Y, (2) other sources of autocorrelated errors and (3) the distributed lag impact of the exogenous variable(s). In the presence of trend and (or) autocorrelation of errors, y, in Eq. (7) cannot be a reliable estimate of the adjustment rate, and, as an implication, the estimates of the dynamic multipliers and the long-run impact multiplier will be distorted as well. The model fails to discriminate between the specification of the error process and the dynamic impact specification.7 King
5 How to proceed if one wants to model different adjustment rates for different exogenous variables is explained in Kmenta (1986, p. 531). 6 And only once were both of them significant in a single equation. These results were confirmed in my own reanalysis of the data when I applied Wald tests to the restrictions. The data set was compiled by King and Laver and made available to me by the ICPSR data archive, University of Michigan, Ann Arbor, via the Zentralarchiv fu¨r empirische Sozialforschung at the Universita¨t Ko¨ln, Germany. Analyses were performed with the econometric package MICROFIT 3.0 (Pesaran and Pesaran, 1991). 7 Clear warnings not to confuse the specification of error structures with specifications of the dynamic impact of an exogenous variable are given, for instance, in Dhrymes (1971, p. 59 cont.) or Maddala (1992, p. 244, 255 cont., 422). For testing problems see also Judge et al. (1985, p, 321 cont.). To wit, separating dynamic impact specification from error autocorrelation and trend is a major concern in the Box–Jenkins modeling approach (Box and Jenkins, 1976), which many econometricians and political scientists like to castigate for is alleged disconcern of substantive issues.
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and Laver (1993, p. 746) report that their estimates of y in 12 equations (for 12 spending categories) were all significant with a single exception: “Commerce & Housing”—which is the only variable showing no clear signs of non-stationarity. If there is a pronounced trend component in Y then there must be a non-zero coefficient attached to Yt−1. “Significant” estimates of y thus should not be read as evidence supporting King and Laver’s theoretical assumptions about partial adjustment mechanisms (which may nevertheless be true). This claim of evidence in favor of the partial adjustment model would indeed be inconsistent with King and Laver’s rejection of the overall model on the basis of non-significant immediate impact multipliers. In their response, Hofferbert et al. (1993) turn King and Laver’s argument upside down by claiming that the large y coefficients support the mandate thesis. Both claims, as they stand now, are unwarranted. If one takes the lagged endogenous variable as representing trend components (rather than being part of the dynamic specification), one is lead to underestimate the impact of the exogenous variables, particularly if they are trending as well. If instead one takes Yt−1 as part of the dynamic specification (although the data are trending), one is likely to overestimate the impact of the Xs. The question therefore remains: How are we to deal with trending data without altering the substance of mandate theory? Some suggestions will be made in the next section.
4. Trend and the concept of cointegration The commonly recommended strategies in dealing with trend components are, first, “detrending” by using some polynomial function or, second, “differencing” the series. Both methods are not feasible in the present case. The trend cannot reasonably be assumed to be deterministic, and differencing a step function (i.e., the platform data) entails some obvious problems. More serious in this context: differencing eliminates or downweights the low-frequency components and thereby suppresses the long-run relationships assumed by mandate theory to exist. This is the major defence of Hofferbert et al. (1993) and Klingemann et al. (1994) in responding to the critique of King and Laver (1993): “The similarity in trends must be retained as part of any statement of the mandate thesis…” (Hofferbert et al., 1993, p. 749). Their argument needs to be taken seriously: any model that does not allow for trend components is not appropriate in testing mandate theory. In essence, Budge and Hofferbert seem to assume that party platforms and spending figures are related to each other in the manner of cointegrated processes (without explicitly referring to this concept). But treating their regression models as cointegrating relationships that should be evaluated as such provokes some immediate objections: the series are too short to test for (non-)stationarity (unit roots), and the stochastic nature of the platform variables is, at least, doubtful. The objections are serious ones; if we consent to them the analysis is bound to end in a stalemate, for it is neither acceptable to ignore the trend problem (and overestimate the impact of party platforms) nor is it acceptable to eliminate trend components from the data or confuse impact and trend parameters (and possibly underestimate the weight of the party platforms). “Cointegration” is the only situation
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where it is legitimate to leave the trend in the data as mandate theory wants to have it. Thus, I propose to use the concept of cointegration as a heuristic means despite the objections just referred to. Data analysis and modeling efforts should not stop where statistical testing ends. In fact, the objections referring to the dubious stochastic nature of the platform variables can be softened by the following considerations. The party platform variables given as sequences of step inputs are just proxy variables. If adequate data on platforms and their continuous interpretation and reinterpretation by the party establishment were available one would get a different picture: the stochastic nature of the underlying process would become visible. This argument rests upon a certain specification of what the term “mandate” means: it would have to allow for the possibility that the public is prepared to modify the programmatic content of the mandate if new circumstances call for new interpretations of old principles. The “stochastic” conception can be further supported by the following argument. If the time unit of analysis would be changed to the 4-year term of the presidential administration (instead of yearly intervals), then the party platforms could directly be treated as stochastic variables. The point estimates would not change, the regression based on the quadrennial observations would produce the same coefficients as those obtained with yearly data (as King and Laver already noted), the standard errors would be corrected. If these arguments are not convincing, i.e., if one still wants to treat the platform variables as non-stochastic, one may take recourse to the notion of a “causal-trends” model as explicated in a paper by Kang (1990). In these models the regressor X is a (possibly non-linear) function of time (i.e., non-stochastic), and Y is a function of X; Y then exhibits trend movements which correspond to those contained in X. The underlying logic is the same as in the case of cointegration with difference stationary series. The coefficients of the linear combination of X and Y can be consistently estimated by an OLS regression of Y on X; the residuals should be stationary. “Causal-trends” and “cointegration” belong to the same family of models. We can thus leave open the question concerning the stochastic nature of the independent variable. No matter which heuristic we apply the crucial test, at any case, is the stationarity of the residuals. This would also hold if we looked at the Budge–Hofferbert model as a way of simply regressing a stochastic variable on a fixed treatment variable, the treatments being the party platforms produced by party conventions. Though the shortness of the series forbids unit root testing to evaluate the stationarity of the residuals, one can (and should) at least look at them. This apparently has not been done by Hofferbert and his collaborators in a systematic way. In some cases it may be hard to arrive at a clear-cut decision, in others it may be quite obvious that the residuals are stationary or non-stationary. This visual inspection of the residual series is the most generous “test” of the Budge–Hofferbert mandate model. If it fails on this account, the model and the theory behind it are in serious trouble. I can give here only a few examples of how this informal inspection of the data might be carried out. Fig. 1 presents an example in which the hypothesis of corresponding trends in budgetary figures and party platforms obviously is not true. Defense spending shares decline sharply from the early 1950s to the late 1970s with an interruption in the
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Fig. 1. Defense Spending, Democrat and Republican platform emphasis.
Fig. 2.
Defense Spending, plot of actual and fitted values.
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mid-1960s. The platform categories (“special foreign relations”) matched to defence spending8 are clearly not in line with the spending trend. Fig. 2 presents the actual and the fitted values from the regression analysis based on the Budge–Hofferbert model. This model obviously fits the data very badly, though three of four slope coefficients are “significant” with adj. R2 ⫽ 0.36. The residuals are clearly non-stationary. If one compares the fitted values with the platform values from which they have been derived it is impossible to “see” a connection.9 The discrepancy is most striking for the 1956 election, when both parties increased their emphasis but the model estimated from these data predicts a decrease—with a complementary error in 1960. This example demonstrates how far off the mark coefficient estimates may be if they have been derived from a misspecified model. At any case, the voters will not interpret the platform signals in the same way as the least-squares algorithm.10 Fig. 3 presents the actual and predicted values from the best-fitting model (adj. R2 ⫽ 0.88) already discussed in Section 2 (“Education & Employment Services”).
Fig. 3.
8
Education & Employment, plot of actual and fitted values.
The platform values were multiplied by a factor of 6 to adjust for level differences. The picture hardly improves if one reruns the regression analysis with the first four years cut off from the series. 10 The authors interpret the assumed structural relationships in terms of the signaling quality of the platform variable: “Our concerns here are…with the signaling capacity of our independent variables… The mandate is essentially a mechanism by which voters have available a set of alternative signals that may be harbingers of alternative future actions” (Klingemann et al., 1994, p. 283). One may wonder, however, if the public perceives the signals as they appear in the estimated regression equations: combined to multiplicative terms and weighted by positive and negative coefficients of widely differing size. 9
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The fit is quite impressive, the residuals (Fig. 4), however, do not appear to be stationary. This deficiency seems to result partly from structural changes and outliers. From 1948 to 1976 both parties’ emphasis on “Education & Employment Services” show a rising overall trend with two spectacular outliers in the Republican series: a sharp rise of emphasis in 1960 and an equally sharp fall in 1964. From 1976 onward Democrats and Republicans diverge on these issues and spending seems to follow more closely the party of the president. If we apply the extended model to these data in order to account for possibly “negative” mandate effects (as explained in Section 3) we get the following results (without time index; t-ratios in parentheses)
The sign of the coefficients for the main and the simple interaction effects are the same as in the B-H model. There are significant “divergence” effects for both parties, but in opposite directions. If Democrats and Republicans have shifted their platform emphasis in diverging directions, the governing Democrats follow their own policy preferences less vigorously than without such a divergence; the governing Republicans however seem to realize a negative mandate effect—in the case of diverging program changes, they pursue their own programmatic goals more forcefully than
Fig. 4.
Education & Employment, plot of residuals.
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without this divergence.11 It is encouraging to note that the residuals of the extended model (not shown) are more in line with the stationarity requirement than the residuals from the original B-H model. These results must be considered with caution; derived from a very small sample, they are merely suggestive. Divergences on education emphasis occurred in 1960, 1964 and 1980. Thus the Republicans governed with a programmatic divergence only once—obviously not a solid base for parameter estimation. A final warning should be added. Hofferbert and his colleagues seem to have been too much impressed by the often very high coefficients of determination they derived from their models (see, e.g., Hofferbert et al., 1993, p. 122). As already indicated, high R-squareds may be very deceptive, if obtained from trending data. The problem is demonstrated in Fig. 5. Fig. 5 clearly shows that there is no positive level relationship between “Social Justice” (as coded from the Democratic and the Republican party platforms) and spending shares on “Health & Medicare”. If anything, there should be a negative relationship (contrary to mandate theory). The least-squares algorithm manages to weight the platform variables and their multiplicative terms in such a way as to produce a fit of R2 ⫽ 0.49 with the B-H model; the fit increases
Fig. 5.
Health & Medicare, expenditures and platform emphases.
11 The extraordinary high estimate of nmr ⫽ 37.9 is due to the fact that platform divergence occurred only once during a Republican incumbency, and it was of very small size (0.006), whereas spending shares rouse quite a bit during this term. Since the slope coefficient refers to a unit change in the regressor, the coefficient had to explode. If one transforms the divergence variable into a simple 1–0 dichotomy (divergence yes or no), the coefficient is reduced to 2.13.
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to a staggering R2 ⫽ 0.79 with the extended model—but both models are nonsense. The platform category of “Social Justice” has also been matched with two other spending categories, “Social Security” and “Income Security”, and the results are nearly identical. The estimated regression equations produce very high “fits”, but the time-series plots (if not the high negative coefficients of the main effects) clearly demonstrate that in these cases there are no level relationships that would support mandate theory.
5. Conclusions The methodological approach followed by Budge and Hofferbert (1990) and Klingemann et al. (1994) has been rightly criticized by King and Laver (1993) for (1) ignoring the problems caused by trending data, and (2) paying no attention to the parameter restrictions implied by the theoretical model. The present paper expands upon these criticisms and adds a third point (Section 2): the formal mandate model should be extended to include a “divergence term” designed to separate the effects of positive and negative mandate in order to avoid conceptual discrepancies presently inherent in the model. The alternative approach recommended by King and Laver (Section 3) offers no adequate solution to the trend problem. The partial adjustment model they propose does not clearly discriminate between the dynamic impact specification and the specification of trend or error autocorrelation. Also, Hofferbert and his collaborators make a valid point by insisting that party mandate theory calls for level relationships between the content of party platforms and governmental output figures. But they fail to recognize that the hypothesized co-movement of trends in these variables cannot merely be presupposed but must be demonstrated empirically. “Cointegration” and “causal-trends” models are particularly tailored towards incorporating trends and testing the legitimacy of doing so. Though formal statistical tests (unit-root tests) cannot, for various reasons, be reliably applied to the given data, I suggest (in Section 4) to apply these models in a heuristic way by closely inspecting the time-series plots for co-movements of trends and for stationarity of residuals. Examples have been given of how these inspections might be performed and which conclusions they might suggest. The empirical evidence gathered in this way from the US data covering the period from 1948 to 1985 seems to speak more strongly against than in favor of the party mandate theory as advanced by Budge, Hofferbert and others. More definitive judgement might be postponed until more data (longer time series) are available and more adequate methods have been applied. In the meantime, a closer and more systematic inspection of the time-series plots should be carried out for all the data collected in different countries by Klingemann et al. (1994). Another suggestion has been made by one of the anonymous reviewers who would like to see the extended mandate model tested with the pooled-cross-sectional timeseries data that are now available. This would increase the number of cases and add a comparative perspective to the analysis. The enriched data base would also allow to add to the model “institutional variables, such as the party system and the presence
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of coalition governments”. This approach, however appealing it is, would again need to tackle the problem of trending data—for each model and each country. Thus, all of the discussion in Section 4 remains relevant. Besides that, it would probably be unrealistic to assume the coefficient vector in a pooled model to be equal across countries. The advantages arising from increased sample size (resulting from pooling) are thus likely to be lowered again. Nevertheless, it would probably be worthwile to make use of the pooled data set.
References Engle, R.F., Granger, C.W.J., 1987. Co-integration and error correction: representation, estimation, and testing. Econometrica 55, 251–276. Banerjee, A., Dolado, J.J., Galbraith, J.W., Hendry, D.F., 1993. Co-Integration, Error Correction, and the Econometric Analysis of Non-Stationary Data. Oxford University Press, Oxford. Beck, N., 1991. Comparing dynamic specifications: the case of presidential approval. In: Stimson, J.A. (Ed.), Political Analysis, vol. 3, The University of Michigan Press, Ann Arbor, MI, pp. 51–87. Box, G.E.P., Jenkins, G.M., 1976. Time Series Analysis. Forecasting and control, 2nd ed. Holden-Day, San Francisco, CA. Budge, I., Hofferbert, R., 1990. Mandates and policy outputs: U.S. party platforms and federal expenditures. American Political Science Review 84, 111–131. Dhrymes, Ph.J., 1971. Distributed Lag. Problems of Estimation and Formulation. Holden-Day, San Francisco, CA. Greene, W.H., 1993. Econometric Analysis, 2nd ed. Maxwell Macmillan, New York. Hofferbert, R.I., Budge, I., McDonald, M.D., 1993. Response to King & Laver 1993. American Political Science Review 87, 747–750. Judge, G.G., Griffiths, W.E., Lee, T., Lu¨tkepol, H., 1985. The Theory and Practice of Econometrics. Wiley, New York, NY. Kang, H., 1990. Common deterministic trends, common factors and cointegration. In: Fomby, Th.B., Rhodes, G.F. Jr. (Eds.), Advances in Econometrics 8, JAI Press, Greenwich, CT and London, pp. 249–269. King, G., 1989. Unifying Political Methodology. The Likelihood Theory of Statistical Inference. Cambridge University Press, Cambridge. King, G., Laver, M., 1993. Party platforms, mandates, and government spending. American Political Science Review 87, 744–747. Klingemann, H.-D., Hofferbert, R., Budge, I., 1994. Parties, Policies, and Democracy. Westview Press, Boulder, CO. Kmenta, J., 1986. Elements of Econometrics, 2nd ed. Macmillan, New York, NY and London. Maddala, G.S., 1992. Introduction to Econometrics, 2nd ed. Macmillan, New York, NY. Nelson, Ch.R., Kang, H., 1984. Pitfalls in the use of time as an explanatory variable in regression. Journal of Business and Economic Statistics 2, 73–82. Pesaran, M.H., Pesaran, B., 1991. Microfit 3.0. An Interactive Econometric Software Package, User Manual. Oxford University Press, Oxford. Stevenson, R.L., 1995. Review of Klingemann/Hofferbert/Budge, “Parties, Policies, and Democracy”. International Journal of Public Opinion Research 7, 185–186.
Party mandate theory and time-series analysis: a methodological comment Helmut Thome* Institut fu¨r Soziologie, Martin-Luther-Universita¨t Halle-Wittenberg, D-06099 Halle (Saale), Germany
Abstract In 1990 Ian Budge and Richard Hofferbert published an article in support of “the doctrine of the party mandate”, using evidence from regression analyses relating the content of postwar US party platforms and governmental outputs in terms of yearly expenditure rates. Their approach was severely criticized by Gary King and Michael Laver (1993) but has been maintained by the authors in a subsequent extension of their analysis to include data from Australia, Canada and seven European States. The present article takes issue with both the approach followed by Budge and Hofferbert and the alternative approach recommended by King and Laver. It is argued that the trend problem has not been adequately dealt with and the formalization of the mandate model lacks conceptual consistency. Three major suggestions emerge from the discussion: (1) the formal mandate model should be extended to include a “divergence term” designed to separate positive from negative mandate effects; (2) the analysis should pay closer attention to the parameter restrictions that follow from the theoretical model; and (3) the regression equations should be interpreted heuristically in terms of “cointegration” or “causal-trends” models. 1999 Elsevier Science Ltd. All rights reserved. Keywords: Party mandate theory; Cointegration models
1. Introduction In 1990 Ian Budge and Richard Hofferbert published an article in support of “the doctrine of the party mandate, according to which the competing parties offer to the voters different governmental programs between which they can choose. The party * Tel.: ⫹ 49-0345-5524260; fax: ⫹ 49-0345-5527149; e-mail: [email protected] 0261-3794/99/$ - see front matter 1999 Elsevier Science Ltd. All rights reserved. PII: S 0 2 6 1 - 3 7 9 4 ( 9 9 ) 0 0 0 1 5 - 3
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which attracts the most votes on this basis then forms the next government, but it is bound…to carry through the program on which it has been elected” (Budge and Hofferbert, 1990, p. 111). By way of regression analyses, they established what they thought to be “strong links” between postwar (1948–1983) election platforms (coded into 54 subject categories indicating programmatic emphases across several issue areas) and governmental outputs (in terms of yearly expenditure shares) in the United States. The methodology Budge and Hofferbert had followed was strongly criticized by Gary King and Michael Laver (1993) who, in their reanalysis of the data, concluded that “party platforms have small or nonexistent effects on government spending”. In their reply to King and Laver’s critique, Hofferbert et al. (1993) defended their original thesis and methodology, arguing that level relationships must be maintained and that “mandates” only involve an “association, not necessarily a causal connection”, between party programs and government policy. This position was also upheld in a book that extended their previous analyses to include data from Australia, Canada and seven European States (Klingemann et al., 1994). In a review of this book it was noted that “[it] is heavy on method and data… It serves as a quiet but powerful reminder of the power of evidence” (Stevenson, 1995, p. 186). Thus it might be appropriate to reconsider the methodological arguments presented by King and Laver versus those presented by Hofferbert and his colleagues, especially since their debate raises more general problems typically involved in time-series analyses of social data. In Section 2, I discuss the “general program model” proposed by Budge and Hofferbert (henceforth called the “B-H model”)1 and suggest an extension of the formal model which should make for a more adequate representation of the theoretical concept. In Section 3 it is argued that the partial adjustment model introduced by King and Laver (1993) does not adequately solve the trend problem which motivated its construction. In Section 4 I argue that Budge and Hofferbert are right in deriving from their theoretical model long-run co-movements between the trending content of party platforms and trending governmental output. These co-movements, however, cannot be simply presupposed but must be demonstrated empirically. I suggest to apply, at least heuristically, “cointegration” or “causal-trends” models, to this task. Concluding remarks follow in Section 5.
2. The Budge–Hofferbert mandate model Like King and Laver I shall focus on the US data and “Model 5”, the mandate model, which “is the one that corresponds most closely to the idealized mandate theory” (Budge and Hofferbert, 1990, p. 120). It is given here in Eq. (1) with minor notational changes: E(Yt ⫹ 2) ⫽ ␣ ⫹ dDt ⫹ rRt ⫹ pdDt·Gt ⫹ prRt(1 ⫺ Gt).
(1)
1 In the original paper the model is also referred to as “model 5”. In the book (Klingemann et al., 1994, pp. 48–51) the same model is called the “agenda plus mandate model” and shortened to “mandate model”.
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Greek letters are parameters to be estimated. Yt+2 represents the percentage of the total US government budget devoted to a specific policy area, like “Education & Employment Services”, in a certain year t ⫹ 2. Dt represents the percentage, two years earlier, of the Democratic party platform that was devoted to a policy area matched to the spending category; Rt refers to the percentage weight of the same policy area in the Republican platform; Gt is a dummy variable which takes on the value of “1” in the years of a Democratic president and “0” in the years of a Republican president. (The variable (1 ⫺ G) thus takes on the value of “0” in the years of a Democratic president and “1” in the years of Republican presidents.) The multiplicative terms have been included to allow for the (hypothesized) possibility that a party’s influence on the federal budget varies depending on whether or not the party holds the presidency. The core assumption of mandate theory is that the winning party, more so than the losing party, should be able (and willing) to pursue policy preferences in accordance with its own party platform. Since party platforms only change every four years the platform variables are recorded as intermittent step changes; four successive years, for example 1952 through 1955, are all given the same value decided upon at the 1952 convention. The estimated parameters therefore indicate the average effect of a percentage shift of a certain platform category over a four-year period under the assumptions (1) that the effect materializes not before the second year following the last party convention, (2) that it extends two years into the next presidential term and (3) that there is an interactive effect linking party platform and presidential office. To give an example, we look at the estimation results for “Education & Employment Services” (see Table 3 in Budge and Hofferbert, 1990, p. 122), which is the regression equation with the highest coefficient of determination (R2 ⫽ 0.88): ˆ d ⫽ 0.66, ˆ r ⫽ ⫺ 0.12, ˆ pd ⫽ 0.55, ˆ pr ⫽ 0.50 where d and r, the main effects, are called “agenda effects” by Klingemann et al. (1994), whereas the multiplicative effects, pd and pr, are called “(pure) mandate effects”; the sum of the party effects—(d ⫹ pd) or (r ⫹ pr)—will be referred to as “total effects” of the party in office. If we accept the model and its parameters as they stand now, the interpretation is as follows. If the Democrats increased (lowered) their platform emphasis on education and the Democratic candidate won the subsequent presidential election, then spending-shares on education increased (decreased) by (0.66% ⫹ 0.55%) ⫽ 1.2% per unit change in the amount of platform content devoted to education. If the losing Republicans had, at the same time, lowered their platform emphasis on education, this would have further increased the expenditure share of education due to the negative weight of ˆ r ⫽ ⫺ 0.12. Klingemann et al. (1994, p. 50 ff.) call this a “negative mandate” effect. It also follows from the estimated parameters that the Democrats, if not in office, still manage (contrary to the Republicans) to move government expenditures on education in the direction of their own programmatic emphasis. For the losing party the multiplicative term is zero. If the Republican Party wins the presidential election, then, according to this model, it will push the spending-share on education with the weight of ˆ r ⫹ ˆ pr ⫽ ( ⫺ 0.12 ⫹ 0.50) ⫽ 0.38 in the direction of its own platform emphasis,
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but the Democrats can outweigh this move with their main effect coefficient of ˆ d ⫽ 0.66 if their programmatic emphasis has changed in the opposite direction. To sum up, d and r give the total effect of the respective “out-party”, ˆ pd and pr “tells us the difference in the translation of program to policy of Party A’s program when that party wins, relative to when it loses” (Klingemann et al., 1994, p. 50). The first point of controversy has been phrased in terms of significance testing, but what really is at issue here are the restrictions that the theoretical hypotheses place upon the model parameters. King and Laver (1993) infer—correctly, I think— from the theory outlined in Budge and Hofferbert (1990) that the total effect for both parties should be positive: (d ⫹ pd) > 0 and (r ⫹ pr) > 0. Consequently, it is not sufficient to test the conditional significance of the main and the interactive effects singly; one needs to estimate the standard error of the total effect (which Budge and Hofferbert, 1990, had not provided). When King and Laver performed adequate tests, they found that only 10 out of 24 total effects (for two parties and 12 spending categories) were significant on the 5% level. One might argue about the appropriate level of significance; but note from Table 1 in King and Laver (1993, p. 747) that 10 of the estimated sums (total effects) are even negative and two of the positive ones are less than 1.2 times larger than their respective standard errors, a third one is only 1.45 times the size of its standard error. Thus, even if we lower the required significance level quite a bit and apply a one-sided test, the model fails in at least half the cases. The actual disconfirmation, however, is even stronger if one takes into account that the model applies to both parties at once and that, for each equation, the restriction should hold that (d ⫹ pd) > 0 and (r ⫹ pr) > 0. This requirement is met by only two of the 12 policy areas for which the B-H model has been tested on US data. Hofferbert and his colleagues apparently want to focus on the interactive effects, pd and pr; i.e., on the “difference in the translation rate of the Republican and Democratic platform, respectively, when that particular party wins relative to when it loses”. They find “in 13 of the 24 instances reanalyzed by King and Laver, winning matters for positive translations of a party’s platform emphases into expenditure priorities. This, we think, is important” (Hofferbert et al., 1993, p. 748). Yet this distribution hardly supports the model; one would expect such a result from a random experiment in which positive and negative outcomes have equal probabilities. Finally, Hofferbert et al. (1993, p. 748) argue: “Second, and more important, one must recognize that a positive coefficient for the winning party’s favoured policy does not necessarily mean that the net spending share increases when the party takes office”. This observation does not affect King and Laver’s argument at all. The expected net change in expenditure share, Yt ⫺ Yt−1, could even be negative if all the coefficients were positive and the winning party had increased its platform emphasis on Y—it could still be negative if the losing party had decreased its platform emphasis to an extent that would outweigh the increased emphasis of the winning party. In their original paper, Budge and Hofferbert explicitly (but erroneously, I think) made the restriction that the main effect coefficients should be negative (Budge and Hofferbert, 1990, p. 119). Later, in the book, this restriction was lifted and negative main effects were interpreted to constitute a special case called “nega-
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tive mandate”. What the authors mean by this is stated in the following way: “Incumbents may have a mandate not only for their own particular programmatic emphases but also against specific other favourite themes of the losers. If Party A’s program stresses welfare and Party B’s stresses defence, when Party A wins, its mandate could be read as both a call for increased welfare and also for decreased defence, on the grounds that the voters’ preferences in voting for Party A may have been either positive (pro welfare) or negative (anti defence). The vote can convey a positive and/or a negative mandate… In the case of the positive mandate, the multiplicative terms (1 ⫻ the program percent for Party n’s emphasis on topic i when in government; 0 when out)—b(Pni ⫻ G)—will have a positive sign (+). In the case of the negative mandate, the simple term—bPni—will have a negative sign (−)” (Klingemann et al., 1994, p. 50 ff.). Note that, according to the second part of this definition, the sign of the main effect of Party A indicates the negative mandate of Party A, and not that of some other Party B. Though the concept of the negative mandate is substantively clear, its operationalization in terms of a negative main effect coefficient is unsatisfactory; it even contradicts the underlying theoretical concept. First, the operational definition is incomplete. If, for some Party A, the main effect is negative and the multiplicative effect is positive, does this mean that A has a negative and a positive mandate? Second, if the negative mandate of the winning Party A arises in reaction to the losing Party B’s opposite shift of policy emphasis (or de-emphasis), how can it be made a function of A’s own platform emphasis as the definition just quoted has it? The answer is, it cannot. In their actual analysis of the US data (now covering the period from 1948 to 1990) Klingemann et al. (1994) use another definition by treating the negative main effect of the losing Party B as being indicative of the negative mandate of the winning Party A. This seems to make sense as long as the winning party and the losing party shift their platform emphasis in opposite directions. Consider again the previously presented example of “Education & Employment” and suppose that the Democratic candidate wins the election, after his party’s platform increased its emphasis on education and the Republicans decreased theirs. In such an instance, one has to expect (from the estimated model given above) a positive shift in the expenditure share of education due to the positive total effect of the Democratic platform shift and an added positive effect resulting from the negative change in Republican emphasis on education weighted by the negative main effect coefficient r. The Republican party, however, is not always the loser; and the model must equally apply to both parties’ winning or losing, increasing or decreasing their emphasis. What can be predicted from the same estimated model, if, for example, the Republicans win the election after de-emphasizing education contrary to what the Democrats do in their platform? Since the main effect estimate is negative, ˆ r ⫽ ⫺ 0.12, de-emphasizing produces a positive change component which must be out-weighted by a positive interactive effect ˆ pr > 0.12 multiplied by a negative change. We again encounter the restriction that the total effect should be positive for both parties, if the mandate model is correct. But now consider a pre-election situation where both parties, the Democrats and the Republicans, increased their emphasis on education. Then a newly installed Democratic
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administration would, according to the model, increase its spending on education less than in the previous situation where the Republican platform moved in the opposite direction. That is, the “negative mandate” of the governing party (as long as it is defined by the negative main effect of the losing party’s platform) implies the expectation that the winning party always acts less in accord with its own party platform if it has the support of the losing party than it would be the case if the losing party’s platform had been changed in the opposite direction. This may indeed happen under special circumstances; but for the general model (which does not specify these circumstances) this implication runs counter to mandate theory. Thus, the restriction must be maintained that neither the main (agenda) nor the multiplicative (mandate) effect should be negative. The concept of a negative mandate has to be operationalized in a different way. One solution to the problem might be the addition of two higher-order multiplicative terms that further specify the effects of incumbency for both parties according to whether or not the winning party’s most recent platform change diverges from (or is congruent with) the most recent change of emphasis in the losing party’s platform. Technically speaking, the multiplicative term D·G in Eq. (1) needs to be multiplied by a second dummy variable, say “NM” (Negative Mandate) which has, in four consecutive years, the value of “1” if in an election year the Democratic and the Republican platform emphases have shifted in opposite direction; if the emphasis shifts of the two parties do not diverge, NM is “0”. Likewise, the multiplicative term R(1 ⫺ G) representing the effect of the Republican presidency needs to be multiplied by the same dummy variable NM. The expanded model is given by Eq. (2): E(Yt ⫹ 2) ⫽ ␣ ⫹ dDt· ⫹ rRt ⫹ pdDt·Gt ⫹ prRt(1 ⫺ G)t
(2)
⫹ dnm(D·G·NM)t ⫹ frm[R(1 ⫺ G)NM]t. The restriction that the parameters r, d, pd and pr should all be positive still applies. The expanded model clearly ties the concept of a “negative mandate” to the occurrence of divergent party platforms (in the sense explained above). Whereas a positive mandate is represented by pd (for the winning Democratic president) or pr (for the winning Republican president), a negative mandate is indicated by dnm > 0 (for the Democratic president) or by dnm > 0 (for the Republican president). Whether or not such positive divergence effects occur is a purely empirical question. The estimates may even be negative without contradicting mandate theory—if only the sum of all three coefficients remains positive for each party. A negative coefficient dnm or rnm tells us that the president’s power to pursue his own party’s programmatic preferences is lowered if the opposition party has shifted its emphasis into the opposite direction. The influence of the losing party’s platform emphasis is indicated by the (positive) main effect, if no “divergence” occurs. If the two platforms diverge, the negative mandate effect of the winning party (e.g., the Democrats) must be taken into account. The (possibly negative) influence of the “out-party” (e.g., the Republicans) is then given by the difference (r ⫺ dnm). Given the shortness of the time series available so far and the very few instances of diverging or converging platform changes between 1948 and 1983 (or even 1990),
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parameter estimation becomes rather hazardous. Nevertheless, an example will be presented at the end of Section 4, after additional problems of modeling and estimation have been discussed. 3. The partial adjustment model proposed by King and Laver King and Laver (1993) address yet another problem which often troubles the timeseries analyst: the presence of pronounced trend components. Budge and Hofferbert (1990) decided to ignore the clear secular trend exhibited in most of the budget figures they have analysed. The platform variables, too, are non-stationary. Trending data violate one of the core assumptions in ordinary least-squares estimation: that the observations are statistically independent from each other. As King and Laver rightly point out, “regressions with trending variables, very high R-squared values, and bad Durbin–Watson statistics are exactly the situation…described [as] ‘spurious regression’” (King and Laver, 1993, p. 745). In such a situation, the coefficient of determination tends to be largely inflated, the estimated standard errors of the regression coefficient are biased and significance tests become unreliable. Budge and Hofferbert (1990, p. 118) report that “various tests conducted on the effects of time as an influence both on emphases and expenditures demonstrate a limited effect that by no means detracts from the independent influence of platform emphases on spending shares”. This empirical result, however, does not indicate that trend has no relevant impact on estimation. If the trend is not deterministic but stochastic (which is rather likely with social and cultural indicators), the inclusion of a time variable into the regression equation makes little difference and does not remove spuriousness from estimation. For example, Nelson and Kang (1984) found out in their experimental studies that independently generated random-walk processes (that, by definition, are stochastic trends), if regressed on each other, produced an average coefficient of determination of R2 ⫽ 0.50. When a time variable was included, the correct null hypothesis of no relationship was still rejected in 64% of all cases, though the level of significance had been set at 5%. Without the inclusion of a time variable Banerjee et al. (1993, p. 74 cont.) established a rejection ratio of 75%. From these and other studies we learn that detrending a series by a polynomial function of time or, equivalently, by including a time variable among the regressors is not an effective control on spuriousness caused by the presence of stochastic trend components. Specific circumstances may be given where trending variables are not harmful: the case of cointegration. Since King and Laver do not discuss this possibility (although it is suggested by party mandate theory) I shall not consider it before Section 4. King and Laver (1993) try to circumvent the trend problem by proposing a new model which substantively differs from the B-H model and also seems to control effectively the impact of trend. They first accept the basic premise of the B-H model that the preferred expenditure share, YP, is a function of the relative amount of emphasis, X, that a certain policy area receives in the party platform:2 2 I give a more elaborate presentation of the model proposed by King and Laver in order to render my subsequent arguments more intelligible. For the following see almost any econometric textbook, e.g., Greene (1993, p. 526 cont.), Maddala (1992, p. 415 cont.) or Kmenta (1986, p. 528 cont.).
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YPt ⫽ ␣ ⫹ Xt ⫹ ⑀t, ⑀t 苲 i.i.d.(0,).
(3)
To simplify derivations, Eq. (3) (and the following ones as well) are written with one regressor variable only; the time lag is also excluded. Note that Eq. (3) states an equilibrium relationship, where  indicates how much change in the preferred spending level eventually arises from a unit change in a party’s platform emphasis. To this model King and Laver add the assumption that the change in the actual level of spending, Yt, does not come about at once (within one time interval) but unfolds gradually.3 More specifically, they assume that Yt is determined by a weighted average of the previous value, Yt−1, and the preferred level Yt ⫽ ␥Yt ⫺ 1 ⫹ (1 ⫺ ␥)YPt , where 0 ⱕ ␥ ⬍ 1
(4)
or, equivalently, (Yt ⫺ Yt ⫺ 1) ⫽ (1 ⫺ ␥)(YPt ⫺ Yt ⫺ 1).
(4a)
The coefficient (1 ⫺ ␥) is called the “adjustment coefficient” since it indicates the rate of adjustment of Yt to YPt . The larger it is the more rapidly Yt moves towards its equilibrium value YPt . Combining Eq. (4a) and (3) gives Yt ⫽ ␣(1 ⫺ ␥) ⫹ (1 ⫺ ␥)Xt ⫹ ␥Yt ⫺ 1 ⫹ (1 ⫺ ␥)⑀t,
(5)
which can be written as Yt ⫽ c ⫹ Xt ⫹ ␥Yt ⫺ 1 ⫹ ut,
(6)
with c ⫽ ␣(1 ⫺ ␥), ⫽ (1 ⫺ ␥) and ut ⫽ (1 ⫺ ␥)⑀t, where ut has the same properties as ⑀t in Eq. (3). From this it follows that the slope of the equilibrium relationship given in Eq. (3) can be retrieved by ˆ ⫽ ˆ /(1 ⫺ ␥ˆ ). It is called the “long-run impact” or “equilibrium” multiplier, whereas is referred to as the “immediate” impact multiplier. Note specifically that “Gamma”, the coefficient of the lagged endogenous variable, Y(t ⫺ 1), has part in it. Eq. (6) is the well-known geometric lag or first-order autoregressive distributed lag model which is open to several (and partly competing) substantive interpretations, the “partial adjustment model” being only one of them.4 King and Laver (1993, p. 746) set up the OLS estimation equation for their partial adjustment model in the following way (with minor notational changes) E(Yt) ⫽ *0 ⫹ *rRt ⫺ 2 ⫹ *dDt ⫺ 2 ⫹ *pd(D·G)t ⫺ 2 ⫹ *pr[D(1 ⫺ G)]t ⫺ 2
(7)
⫹ yYt ⫺ 1.
3 Remember that Budge and Hofferbert assumed a two-year delay before a new president could influence the budget. 4 Cf. Beck (1991) and King (1989, ch. 7). On the mathematical equivalence of substantively diverging models, also see Banerjee et al. (1993, p. 48 cont.).
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Eq. (7) differs from the B-H model in Eq. (1) merely by the added endogenous term Yt−1; it does not include the “divergence term” introduced in Section 2. If only one endogenous term with lag k ⫽ 1 appears on the right-hand side it has to “take care” equally of all the exogenous variables in the equation which, in this case, implies (1) the assumption of identical adjustment rates (equal speed, but not equal amounts) for the winning and the losing party in transferring their platform changes (positively or negatively) into changes of expenditure shares in the federal budget.5 With the platform levels fixed to the same value for four consecutive years and the given time lag of k ⫽ 2, the model also implies (2) that the impact of a platform change will gradually build up and reach its highest level two years after the end of the presidential term for which the platform had been set up. One wonders if these two assumptions approximate reality more closely than Budge and Hofferbert’s estimation of an average impact for the same four-year period. This is a substantive issue that I shall not discuss here. King and Laver claim that their model “eliminates…most of the problems with autocorrelation and nonstationarity” (King and Laver, 1993, p. 746). Their major concern is the statistical significance of the immediate impact multiplier. They report that only four of the 24 sums of estimated coefficients—(ˆ d ⫹ ˆ pd) and (ˆ r ⫹ ˆ pr)— turned out to be significant on the 5% level.6 The major problem with their approach is that the parameters of the partial adjustment model (just like those of any other dynamic model) cannot be adequately estimated and tested with non-stationary data (Kmenta, 1986, p. 531)—unless the processes are “co-integrated” (see Section 4 below) and the partial adjustment model becomes the “error correction” part in a more comprehensive model (Engle and Granger, 1987; Maddala, 1992, p. 420; Beck, 1991). Consider again the coefficient of the lagged endogenous variable: it is “overburdened” with representing (and confusing) three types of effects originating from (1) the trend in Y, (2) other sources of autocorrelated errors and (3) the distributed lag impact of the exogenous variable(s). In the presence of trend and (or) autocorrelation of errors, y, in Eq. (7) cannot be a reliable estimate of the adjustment rate, and, as an implication, the estimates of the dynamic multipliers and the long-run impact multiplier will be distorted as well. The model fails to discriminate between the specification of the error process and the dynamic impact specification.7 King
5 How to proceed if one wants to model different adjustment rates for different exogenous variables is explained in Kmenta (1986, p. 531). 6 And only once were both of them significant in a single equation. These results were confirmed in my own reanalysis of the data when I applied Wald tests to the restrictions. The data set was compiled by King and Laver and made available to me by the ICPSR data archive, University of Michigan, Ann Arbor, via the Zentralarchiv fu¨r empirische Sozialforschung at the Universita¨t Ko¨ln, Germany. Analyses were performed with the econometric package MICROFIT 3.0 (Pesaran and Pesaran, 1991). 7 Clear warnings not to confuse the specification of error structures with specifications of the dynamic impact of an exogenous variable are given, for instance, in Dhrymes (1971, p. 59 cont.) or Maddala (1992, p. 244, 255 cont., 422). For testing problems see also Judge et al. (1985, p, 321 cont.). To wit, separating dynamic impact specification from error autocorrelation and trend is a major concern in the Box–Jenkins modeling approach (Box and Jenkins, 1976), which many econometricians and political scientists like to castigate for is alleged disconcern of substantive issues.
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and Laver (1993, p. 746) report that their estimates of y in 12 equations (for 12 spending categories) were all significant with a single exception: “Commerce & Housing”—which is the only variable showing no clear signs of non-stationarity. If there is a pronounced trend component in Y then there must be a non-zero coefficient attached to Yt−1. “Significant” estimates of y thus should not be read as evidence supporting King and Laver’s theoretical assumptions about partial adjustment mechanisms (which may nevertheless be true). This claim of evidence in favor of the partial adjustment model would indeed be inconsistent with King and Laver’s rejection of the overall model on the basis of non-significant immediate impact multipliers. In their response, Hofferbert et al. (1993) turn King and Laver’s argument upside down by claiming that the large y coefficients support the mandate thesis. Both claims, as they stand now, are unwarranted. If one takes the lagged endogenous variable as representing trend components (rather than being part of the dynamic specification), one is lead to underestimate the impact of the exogenous variables, particularly if they are trending as well. If instead one takes Yt−1 as part of the dynamic specification (although the data are trending), one is likely to overestimate the impact of the Xs. The question therefore remains: How are we to deal with trending data without altering the substance of mandate theory? Some suggestions will be made in the next section.
4. Trend and the concept of cointegration The commonly recommended strategies in dealing with trend components are, first, “detrending” by using some polynomial function or, second, “differencing” the series. Both methods are not feasible in the present case. The trend cannot reasonably be assumed to be deterministic, and differencing a step function (i.e., the platform data) entails some obvious problems. More serious in this context: differencing eliminates or downweights the low-frequency components and thereby suppresses the long-run relationships assumed by mandate theory to exist. This is the major defence of Hofferbert et al. (1993) and Klingemann et al. (1994) in responding to the critique of King and Laver (1993): “The similarity in trends must be retained as part of any statement of the mandate thesis…” (Hofferbert et al., 1993, p. 749). Their argument needs to be taken seriously: any model that does not allow for trend components is not appropriate in testing mandate theory. In essence, Budge and Hofferbert seem to assume that party platforms and spending figures are related to each other in the manner of cointegrated processes (without explicitly referring to this concept). But treating their regression models as cointegrating relationships that should be evaluated as such provokes some immediate objections: the series are too short to test for (non-)stationarity (unit roots), and the stochastic nature of the platform variables is, at least, doubtful. The objections are serious ones; if we consent to them the analysis is bound to end in a stalemate, for it is neither acceptable to ignore the trend problem (and overestimate the impact of party platforms) nor is it acceptable to eliminate trend components from the data or confuse impact and trend parameters (and possibly underestimate the weight of the party platforms). “Cointegration” is the only situation
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where it is legitimate to leave the trend in the data as mandate theory wants to have it. Thus, I propose to use the concept of cointegration as a heuristic means despite the objections just referred to. Data analysis and modeling efforts should not stop where statistical testing ends. In fact, the objections referring to the dubious stochastic nature of the platform variables can be softened by the following considerations. The party platform variables given as sequences of step inputs are just proxy variables. If adequate data on platforms and their continuous interpretation and reinterpretation by the party establishment were available one would get a different picture: the stochastic nature of the underlying process would become visible. This argument rests upon a certain specification of what the term “mandate” means: it would have to allow for the possibility that the public is prepared to modify the programmatic content of the mandate if new circumstances call for new interpretations of old principles. The “stochastic” conception can be further supported by the following argument. If the time unit of analysis would be changed to the 4-year term of the presidential administration (instead of yearly intervals), then the party platforms could directly be treated as stochastic variables. The point estimates would not change, the regression based on the quadrennial observations would produce the same coefficients as those obtained with yearly data (as King and Laver already noted), the standard errors would be corrected. If these arguments are not convincing, i.e., if one still wants to treat the platform variables as non-stochastic, one may take recourse to the notion of a “causal-trends” model as explicated in a paper by Kang (1990). In these models the regressor X is a (possibly non-linear) function of time (i.e., non-stochastic), and Y is a function of X; Y then exhibits trend movements which correspond to those contained in X. The underlying logic is the same as in the case of cointegration with difference stationary series. The coefficients of the linear combination of X and Y can be consistently estimated by an OLS regression of Y on X; the residuals should be stationary. “Causal-trends” and “cointegration” belong to the same family of models. We can thus leave open the question concerning the stochastic nature of the independent variable. No matter which heuristic we apply the crucial test, at any case, is the stationarity of the residuals. This would also hold if we looked at the Budge–Hofferbert model as a way of simply regressing a stochastic variable on a fixed treatment variable, the treatments being the party platforms produced by party conventions. Though the shortness of the series forbids unit root testing to evaluate the stationarity of the residuals, one can (and should) at least look at them. This apparently has not been done by Hofferbert and his collaborators in a systematic way. In some cases it may be hard to arrive at a clear-cut decision, in others it may be quite obvious that the residuals are stationary or non-stationary. This visual inspection of the residual series is the most generous “test” of the Budge–Hofferbert mandate model. If it fails on this account, the model and the theory behind it are in serious trouble. I can give here only a few examples of how this informal inspection of the data might be carried out. Fig. 1 presents an example in which the hypothesis of corresponding trends in budgetary figures and party platforms obviously is not true. Defense spending shares decline sharply from the early 1950s to the late 1970s with an interruption in the
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Fig. 1. Defense Spending, Democrat and Republican platform emphasis.
Fig. 2.
Defense Spending, plot of actual and fitted values.
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mid-1960s. The platform categories (“special foreign relations”) matched to defence spending8 are clearly not in line with the spending trend. Fig. 2 presents the actual and the fitted values from the regression analysis based on the Budge–Hofferbert model. This model obviously fits the data very badly, though three of four slope coefficients are “significant” with adj. R2 ⫽ 0.36. The residuals are clearly non-stationary. If one compares the fitted values with the platform values from which they have been derived it is impossible to “see” a connection.9 The discrepancy is most striking for the 1956 election, when both parties increased their emphasis but the model estimated from these data predicts a decrease—with a complementary error in 1960. This example demonstrates how far off the mark coefficient estimates may be if they have been derived from a misspecified model. At any case, the voters will not interpret the platform signals in the same way as the least-squares algorithm.10 Fig. 3 presents the actual and predicted values from the best-fitting model (adj. R2 ⫽ 0.88) already discussed in Section 2 (“Education & Employment Services”).
Fig. 3.
8
Education & Employment, plot of actual and fitted values.
The platform values were multiplied by a factor of 6 to adjust for level differences. The picture hardly improves if one reruns the regression analysis with the first four years cut off from the series. 10 The authors interpret the assumed structural relationships in terms of the signaling quality of the platform variable: “Our concerns here are…with the signaling capacity of our independent variables… The mandate is essentially a mechanism by which voters have available a set of alternative signals that may be harbingers of alternative future actions” (Klingemann et al., 1994, p. 283). One may wonder, however, if the public perceives the signals as they appear in the estimated regression equations: combined to multiplicative terms and weighted by positive and negative coefficients of widely differing size. 9
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The fit is quite impressive, the residuals (Fig. 4), however, do not appear to be stationary. This deficiency seems to result partly from structural changes and outliers. From 1948 to 1976 both parties’ emphasis on “Education & Employment Services” show a rising overall trend with two spectacular outliers in the Republican series: a sharp rise of emphasis in 1960 and an equally sharp fall in 1964. From 1976 onward Democrats and Republicans diverge on these issues and spending seems to follow more closely the party of the president. If we apply the extended model to these data in order to account for possibly “negative” mandate effects (as explained in Section 3) we get the following results (without time index; t-ratios in parentheses)
The sign of the coefficients for the main and the simple interaction effects are the same as in the B-H model. There are significant “divergence” effects for both parties, but in opposite directions. If Democrats and Republicans have shifted their platform emphasis in diverging directions, the governing Democrats follow their own policy preferences less vigorously than without such a divergence; the governing Republicans however seem to realize a negative mandate effect—in the case of diverging program changes, they pursue their own programmatic goals more forcefully than
Fig. 4.
Education & Employment, plot of residuals.
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without this divergence.11 It is encouraging to note that the residuals of the extended model (not shown) are more in line with the stationarity requirement than the residuals from the original B-H model. These results must be considered with caution; derived from a very small sample, they are merely suggestive. Divergences on education emphasis occurred in 1960, 1964 and 1980. Thus the Republicans governed with a programmatic divergence only once—obviously not a solid base for parameter estimation. A final warning should be added. Hofferbert and his colleagues seem to have been too much impressed by the often very high coefficients of determination they derived from their models (see, e.g., Hofferbert et al., 1993, p. 122). As already indicated, high R-squareds may be very deceptive, if obtained from trending data. The problem is demonstrated in Fig. 5. Fig. 5 clearly shows that there is no positive level relationship between “Social Justice” (as coded from the Democratic and the Republican party platforms) and spending shares on “Health & Medicare”. If anything, there should be a negative relationship (contrary to mandate theory). The least-squares algorithm manages to weight the platform variables and their multiplicative terms in such a way as to produce a fit of R2 ⫽ 0.49 with the B-H model; the fit increases
Fig. 5.
Health & Medicare, expenditures and platform emphases.
11 The extraordinary high estimate of nmr ⫽ 37.9 is due to the fact that platform divergence occurred only once during a Republican incumbency, and it was of very small size (0.006), whereas spending shares rouse quite a bit during this term. Since the slope coefficient refers to a unit change in the regressor, the coefficient had to explode. If one transforms the divergence variable into a simple 1–0 dichotomy (divergence yes or no), the coefficient is reduced to 2.13.
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to a staggering R2 ⫽ 0.79 with the extended model—but both models are nonsense. The platform category of “Social Justice” has also been matched with two other spending categories, “Social Security” and “Income Security”, and the results are nearly identical. The estimated regression equations produce very high “fits”, but the time-series plots (if not the high negative coefficients of the main effects) clearly demonstrate that in these cases there are no level relationships that would support mandate theory.
5. Conclusions The methodological approach followed by Budge and Hofferbert (1990) and Klingemann et al. (1994) has been rightly criticized by King and Laver (1993) for (1) ignoring the problems caused by trending data, and (2) paying no attention to the parameter restrictions implied by the theoretical model. The present paper expands upon these criticisms and adds a third point (Section 2): the formal mandate model should be extended to include a “divergence term” designed to separate the effects of positive and negative mandate in order to avoid conceptual discrepancies presently inherent in the model. The alternative approach recommended by King and Laver (Section 3) offers no adequate solution to the trend problem. The partial adjustment model they propose does not clearly discriminate between the dynamic impact specification and the specification of trend or error autocorrelation. Also, Hofferbert and his collaborators make a valid point by insisting that party mandate theory calls for level relationships between the content of party platforms and governmental output figures. But they fail to recognize that the hypothesized co-movement of trends in these variables cannot merely be presupposed but must be demonstrated empirically. “Cointegration” and “causal-trends” models are particularly tailored towards incorporating trends and testing the legitimacy of doing so. Though formal statistical tests (unit-root tests) cannot, for various reasons, be reliably applied to the given data, I suggest (in Section 4) to apply these models in a heuristic way by closely inspecting the time-series plots for co-movements of trends and for stationarity of residuals. Examples have been given of how these inspections might be performed and which conclusions they might suggest. The empirical evidence gathered in this way from the US data covering the period from 1948 to 1985 seems to speak more strongly against than in favor of the party mandate theory as advanced by Budge, Hofferbert and others. More definitive judgement might be postponed until more data (longer time series) are available and more adequate methods have been applied. In the meantime, a closer and more systematic inspection of the time-series plots should be carried out for all the data collected in different countries by Klingemann et al. (1994). Another suggestion has been made by one of the anonymous reviewers who would like to see the extended mandate model tested with the pooled-cross-sectional timeseries data that are now available. This would increase the number of cases and add a comparative perspective to the analysis. The enriched data base would also allow to add to the model “institutional variables, such as the party system and the presence
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of coalition governments”. This approach, however appealing it is, would again need to tackle the problem of trending data—for each model and each country. Thus, all of the discussion in Section 4 remains relevant. Besides that, it would probably be unrealistic to assume the coefficient vector in a pooled model to be equal across countries. The advantages arising from increased sample size (resulting from pooling) are thus likely to be lowered again. Nevertheless, it would probably be worthwile to make use of the pooled data set.
References Engle, R.F., Granger, C.W.J., 1987. Co-integration and error correction: representation, estimation, and testing. Econometrica 55, 251–276. Banerjee, A., Dolado, J.J., Galbraith, J.W., Hendry, D.F., 1993. Co-Integration, Error Correction, and the Econometric Analysis of Non-Stationary Data. Oxford University Press, Oxford. Beck, N., 1991. Comparing dynamic specifications: the case of presidential approval. In: Stimson, J.A. (Ed.), Political Analysis, vol. 3, The University of Michigan Press, Ann Arbor, MI, pp. 51–87. Box, G.E.P., Jenkins, G.M., 1976. Time Series Analysis. Forecasting and control, 2nd ed. Holden-Day, San Francisco, CA. Budge, I., Hofferbert, R., 1990. Mandates and policy outputs: U.S. party platforms and federal expenditures. American Political Science Review 84, 111–131. Dhrymes, Ph.J., 1971. Distributed Lag. Problems of Estimation and Formulation. Holden-Day, San Francisco, CA. Greene, W.H., 1993. Econometric Analysis, 2nd ed. Maxwell Macmillan, New York. Hofferbert, R.I., Budge, I., McDonald, M.D., 1993. Response to King & Laver 1993. American Political Science Review 87, 747–750. Judge, G.G., Griffiths, W.E., Lee, T., Lu¨tkepol, H., 1985. The Theory and Practice of Econometrics. Wiley, New York, NY. Kang, H., 1990. Common deterministic trends, common factors and cointegration. In: Fomby, Th.B., Rhodes, G.F. Jr. (Eds.), Advances in Econometrics 8, JAI Press, Greenwich, CT and London, pp. 249–269. King, G., 1989. Unifying Political Methodology. The Likelihood Theory of Statistical Inference. Cambridge University Press, Cambridge. King, G., Laver, M., 1993. Party platforms, mandates, and government spending. American Political Science Review 87, 744–747. Klingemann, H.-D., Hofferbert, R., Budge, I., 1994. Parties, Policies, and Democracy. Westview Press, Boulder, CO. Kmenta, J., 1986. Elements of Econometrics, 2nd ed. Macmillan, New York, NY and London. Maddala, G.S., 1992. Introduction to Econometrics, 2nd ed. Macmillan, New York, NY. Nelson, Ch.R., Kang, H., 1984. Pitfalls in the use of time as an explanatory variable in regression. Journal of Business and Economic Statistics 2, 73–82. Pesaran, M.H., Pesaran, B., 1991. Microfit 3.0. An Interactive Econometric Software Package, User Manual. Oxford University Press, Oxford. Stevenson, R.L., 1995. Review of Klingemann/Hofferbert/Budge, “Parties, Policies, and Democracy”. International Journal of Public Opinion Research 7, 185–186.