Why do Legislators Skip Votes? Position Taking Versus Policy Influence

The data set and replication code are posted online at http://​goodliffe.​byu.​edu/​papers/​absenteeism.​replication.​zip.

See http://​www.​utsandiego.​com/​news/​2012/​may/​10/​filner-fletcher-missing-many-votes/​.

See http://​cincinnati.​com/​blogs/​nkypolitics/​2012/​04/​11/​coast-calls-out-webb-edgington-on-missed-votes/​.

See http://​atr.​rollcall.​com/​utah-freedom-path-ad-hits-dan-liljenquist-for-missed-votes/​.

See http://​www.​columbian.​com/​weblogs/​political-beat/​2012/​sep/​26/​examining-bentons-missed-votes-defense/​.

A few examples from 2012: Connie Mack was asked to “explain how you don’t show up to work.” Bob Filner was accused of having “one of the worst attendance records in Congress.” Debbie Wasserman Shultz was reportedly “more concerned with headlining fundraisers for [Obama than]…with fulfilling the responsibilities owed to her constituents.” Mazie Hirono was called out for missing “127 votes in Congress.” Gwen Moore was called “Wisconsin’s most absent member of Congress.” Ron Paul and Michele Bachmann were criticized for skipping votes while campaigning for president.

See http://​www.​factcheck.​org/​2008/​09/​obamas-legislative-record/​.

See Noury (2004) for an application to the European Parliament, and Rothenberg and Sanders (2000) for an application to the US Congress.

There is a third difference: In contrast to a mass election, a legislative vote involves few enough participants that a legislator’s decision to abstain may change the ideological location of the legislature’s median voter sufficiently to change the vote outcome. Arguments in Rohde (1991) and Cox and McCubbins (2005) suggest this occurs infrequently in the US House, however. If majority party leaders worried that such a situation was imminent, they could avoid an unfavorable outcome either by keeping the bill off the floor or by using disciplined procedural votes to create an environment where electorally-threatened legislators could safely abstain (or even vote against their party leadership) on substantive votes. Still, Rothenberg and Sanders (2002) find that members of Congress occasionally miss votes when their participation could have been pivotal. Moreover, these Congressional theories may not apply in all state legislatures, where procedural powers vary widely (see e.g. Kim and Phillips 2009; Cox et al. 2010). Future research could profitably assess whether and how often absenteeism in state legislatures actually reverses policy outcomes.

Raising the specter of shirking as an additional cause of absenteeism suggests entirely new theoretical avenues. A small literature, summarized well in Feher and Titiunik (2014), has been particularly interested in how term limits impact shirking. We do not address term limits here, partly because term limits are orthogonal to our core theoretical concerns, and partly because Feher and Titiunik have already presented persuasive evidence that term limits do not increase abstention rates. If there is any effect, the legislator random effects should incorporate the term limit effect.

We rely on the Sunlight Foundation’s coding here; we discuss our dataset further below.

Rothenberg and Sanders (1999) used a dummy for Congressional Quarterly’s key votes. Forgette and Sala (1999) proxied major bills as votes in which each party’s leadership team voted against the other party’s leaders.

We consider only primary sponsorship, not cosponsorship, since states vary widely in their rules and reporting of cosponsorship.

In many states, abstention rules could conceivably vary across chambers. In practice, however, there were no states in our data where the upper and lower chambers had adopted different rules. As a result, we treat abstention rules as a state-level variable.

We include indicator variables for the election cohort.

It appears that most voting events with absentee rates above 50% were committee votes miscoded as floor votes.

We dropped legislators who cast fewer than 20 votes or with an absentee rate above 50%. It appears that most legislators in these circumstances were experiencing serious illnesses or other irrelevant issues that kept them from the legislature for extended periods.

A listing of the missing states and chambers shows no obvious pattern. There are states with large and small populations, and states in all areas of the country. For every state or chamber that we have missing, there is a similar state or chamber in our data set (e.g. South Dakota for North Dakota), except perhaps Hawaii.

The median absentee rate was 0 in these chambers, but there is still sufficient variance for analysis; in each of these chambers, at least 40% of legislators missed at least one vote, with some missing far more.

Utah is among the few states requiring legislators to participate in all votes, even when there is a conflict of interest. That Utah nevertheless has such a high absenteeism rate bolsters our claim that absenteeism and abstention are comparable.

Some states limit the number of session days, while others impose a limit on the number of calendar days (including weekends) that may pass between the session’s first and last day. In states using a calendar day standard, we follow common practice by multiplying the session length (in days) by 5/7 to estimate the number of weekdays in session. Another (uncommon) approach to measuring session length would be to determine the number of distinct dates that appear in our roll call data. Doing so would precisely estimate the number of days when legislators convened on the voting floor. The difficulty is that legislators might convene for committee hearings on a particular day without convening on the floor, producing an underestimate of session length. In our analysis, we stick with the literature’s standard measure of session length. (The two measures correlate at r = 0.22, p = 0.08.).

Because states vary in their use of single and multimember districts (MMD), we use each legislator’s percentage share of the overall vote instead of the vote margin. Out of abundance of caution, we include additional dummies for MMD (interacted with vote share) and for year of election, though these controls turn out to bear little weight.

Because leadership structures vary widely by state, our “leadership” variable captures dichotomously whether Project VoteSmart records the legislator as serving in any leadership position during 2011.

Separate analysis of each level of analysis may be found in a supplemental appendix. These level-by-level regressions produce the same general results as those presented here, with a few minor differences at the margins. Because separate regressions by level of analysis do not account for the nested and crossed structure of the data, however, we do not have confidence that the models reported in the supplement satisfy the Gauss-Markov requirements for OLS to produce unbiased results. Using clustered standard errors (as we do in the supplement) helps account for some of the problems that arise, but it cannot account for all of them.

It also avoids the atomistic fallacy of doing the reverse.

For more on the reasons to use multilevel modeling, see Gelman and Hill (2007).

We use the lme4 package in R (Bates et al. 2015), which handles (partially) crossed and nested random effects elegantly. With 2.9 million observations, five random effects, and up to 31 covariates, some models took several days to run (on a server with 384 GB RAM and 32 cores).

We have nested random effects because legislators are nested within chambers, and thus the legislator random effects are nested within chamber random effects. We have crossed random effects because votes are not nested within legislators. Bates (2010) calls our model “partially crossed,” rather than “completely crossed” because every legislator is not observed with every vote. By comparison to the econometric panel literature, a (completely) crossed random effects model is also called a (balanced) two-way random effects model, with a random effect for entities and a random effect for time.

Like most multilevel models, we assume a normal distribution of random effects. We can then calculate the range of log-odds as \({\text{Intercept}} \pm 1.96 {\text{SD}}\left( {\text{random effect}} \right)\), and convert to probabilities (and percentages). For legislators, the range of log-odds is \(- 4.49 \pm 1.96\left( {1.44} \right)\). The range of probability is then \(1/\left\{ {1 + \exp \left[ { - \left( { - 4.49 \pm 1.96\left( {1.44} \right)} \right)} \right]} \right\}\). Since the average log-odds is the intercept (\(= - 4.49\)), the baseline probability of abstention is \(1/\left\{ {1 + \exp \left[ { - \left( { - 4.49} \right)} \right]} \right\} = 0.011\) or 1.1%.

Table B2 in the supplemental appendix provides less ambivalent results: When analyzing the data at the level of voting events, all four of these indicators have positive coefficients (i.e. absenteeism increases on major bills), and three attain statistical significance.

We also measured legislative salary relative to the state median (logged). Like absolute salary, it was statistically insignificant.

Research on executive vetoes suggests that presidents exercise more vetoes when Congress passes more objectionable bills (Rohde and Simon 1985). Likewise, minority legislators may abstain more often simply out of protest over the bills being brought to the floor. We thank an anonymous reviewer for this insight.

This variable’s substantively small effect works in favor of our decision to treat absenteeism and abstention together. After all, holding many votes in a single day should not affect abstention rates, but the consequences of leaving the chamber for 2 hours would be much greater on a day with more votes. If the two behaviors had identical causes, we would expect no effect on this variable; if they had very different causes, we would estimate a large effect. Getting only a small effect (refer also to Table 2) provides some reassurance that absenteeism and abstention have similar underlying causes.

Since we have almost 3 million observations, the effective degrees of freedom of a variable is the number of entities at the level the variable is measured (Snijders 2005). Thus, there are about 43,450 degrees of freedom for our vote margin variable, which is quite a lot, but not nearly as large as 2.9 million. There are about 35 degrees of freedom for our state-level variables, such as abstention rules. (In a Monte Carlo study, Bryan and Jenkins (2016) recommend at least 30 groups for reliable estimates in multilevel logit models.) Most other variables have effective degrees of freedom between those two levels. The only variables that have 2.9 million degrees of freedom are whether a legislator is voting on his or her sponsored bill, and the cross-level interactions. Because some of these interactions are not significant, sample size alone is not driving statistical significance.

The scatterplot is in Figure B3 of the supplemental appendix. A single-level model of chambers (controlling for other chamber- and state-level factors) shows a negative, but statistically insignificant relationship between absenteeism and session length. Including the interaction uncovers the effect of session length.

We calculate this using the odds ratio \(= { \exp }\left( {\hat{\beta }\Delta x} \right)\), where \(\hat{\beta }\) is the coefficient on \(x\) and \(\Delta x\) is the two standard deviation increase. The percentage change is \(100\% \times \left( {\exp \left( {\hat{\beta }\Delta x} \right) - 1} \right)\). To take into account the effect of the interactive variable, we calculate two values: where the other constituent variable is set to the 10^th and 90^th percentiles.

For a perfectly balanced binary variable—half of the observations at 0, half at 1—a move from 0 to 1 is the same as a two standard deviation shift. (The proportion of Republicans is 0.53.) For unbalanced binary variables, a move from 0 to 1 is greater than two standard deviations. (The proportion of appropriation bills is 0.006. Moving from 0 to 1 is over 12 standard deviations.)

\({\text{odds}} = \frac{p}{1 - p} \approx p\), for small \(p\).

The standard deviation of vote margin is 30.6, and the coefficient is −0.0062. The percentage change in odds (≈ probability) is \(100\% \times \left[ {\exp \left( { - 0.0062 \times 30.6 \times 2} \right) - 1} \right] = - 32\% ;100\% \times \left[ {\exp \left( { - 0.0062 \times 30.6 \times - 2} \right) - 1} \right] = 46\%\).

The vote margin variable is also estimated with precision in each model: its t-statistic (i.e. coefficient/standard error or z-value) is always greater than 10. As noted below, when we exclude strategic votes, legislative vote margin is statistically insignificant.

The single-level model and a scatterplot showing this relationship is found in the supplemental appendix, Table B2 and Figure B2.

Although this is quite large, it is similar in magnitude to the unconditional change in the null model from 1.1% (mean) to 16% (+2 standard deviations).

The residual ICC \(= {\text{variance}}\left( {{\text{random}} {\text{effect}}_{i} } \right)/\left[ {\mathop \sum \limits_{j} {\text{variance}}\left( {{\text{random}} {\text{effect}}_{j} } \right) + \left( {\pi^{2} /3} \right)} \right]\), where \(\left( {\pi^{2} /3} \right) = 3.29\) is the residual variance of a logit model. For legislators, \({\text{ICC}} = \left[ {1.44^{2} + 0.91^{2} + 0.97^{2} } \right]/\left[ {1.44^{2} + 0.91^{2} + 0.97^{2} + 0.59^{2} + 0.42^{2} + 3.29} \right] = 0.50\). We include the state and chamber random effects because legislators are nested within chambers and states. For bills, \({\text{ICC}} = \left[ {0.42^{2} + 0.91^{2} } \right]/\left[ {1.44^{2} + 0.91^{2} + 0.97^{2} + 0.59^{2} + 0.42^{2} + 3.29} \right] = 0.13\). We include the state random effect because bills are nested within states (but not chambers).

This is the conditional mode (i.e. maximum likelihood) of the probability density evaluated at the parameter estimates of the independent variables for each entity.

In the supplemental appendix, we present caterpillar plots for the Full Model including Age. They are qualitatively similar demonstrating that it is not omitting age that leads to the strong random effects, it is other unobservable factors.

In the supplemental appendix, we present the results of the Full Model with Age, and the results of Null and Final Model using the subset of legislator-votes that have legislators’ ages. The results are qualitatively similar, particularly in the key theoretical variables of vote margin and type of bill.

The other variables have similar effects, except for number of votes held that day. Once we control for the percentage of votes missed by a legislator that day, days with more votes have more abstentions.