Social Influence and Legislative Behavior

Legislators have a difficult job. They deal with uncertainty and limited resources, yet participate in hundreds or thousands of votes per term. One coping strategy is to rely on cues (Kingdon Reference Kingdon1973; Matthews and Stimson Reference Matthews and Stimson1975). Cue-takingFootnote ¹ is a diffusion process that subsumes an array of mechanisms, such as imitation, coercion, and learning (Lindstädt, Vander Wielen, and Green Reference Lindstädt, Wielen and Green2016). Cues may be purposively disseminated by parties (Hershberger, Minozzi, and Volden Reference Hershberger, Minozzi and Volden2018; Minozzi and Volden Reference Minozzi and Volden2013), interest groups (Box-Steffensmeier, Christenson, and Craig Reference Box-Steffensmeier, Christenson and Craig2019), senior colleagues (Box-Steffensmeier, Ryan, and Sokhey Reference Box-Steffensmeier, Ryan and Sokhey2015), member organizations (Ringe, Victor, and Carman Reference Ringe, Victor and Carman2013), or peers (Zelizer Reference Zelizer2019).

Cues may also be passed informally between legislators who socialize together. Such cue-taking is more likely to be incidental than purposive. Elites share many behaviors with members of the mass public (e.g., Sheffer et al. Reference Sheffer, Loewen, Suroka, Walgrave and Sheafer2018), among whom informal political discussion is often an incidental byproduct of opportunity (Minozzi et al. Reference Minozzi, Song, David, Neblo and Ognyanova2020). Contact provides opportunity for cues via informal discussion—even among elites. Indeed, physical proximity fosters social ties among legislators (Caldeira and Patterson Reference Caldeira and Patterson1987), and there is evidence of cue-taking between legislators who are merely proximate. Masket (Reference Masket2008) shows that California state legislators who were desk mates agreed on more votes, and Liu and Srivastava (Reference Liu and Srivastava2015) find that copartisan U.S. senators with proximate desks were more ideologically similar. Thus, informal, incidental cue-taking should be more likely given sustained contact.

Contact alone is not sufficient for proximity-based cue-taking, however. The ambient political environment includes an array competing sources of cues (parties, interest groups, etc.). Competition limits the chances that a single source has an effect. Regardless of the mechanism, a multiplicity of cues makes it less likely that any single vector carries much signal. Not only does competition pose a theoretical challenge to any particular sort of cue-taking, it complicates the inferential problem, since weaker signals are more difficult to detect. Consequently, cue-taking should be more likely to occur and be observable in environments with less competition.

Although the theoretical case for social influence among legislators is compelling, uncovering empirical evidence of influence is complicated by its causal complement: homophily. Homophily refers to tie formation between similar individuals, the tendency for “birds of feather to flock together” (McPherson, Smith-Lovin, and Cook Reference McPherson, Smith-Lovin and Cook2001). Influence and homophily are confounded (Fowler et al. Reference Fowler, Heaney, Nickerson, Padgett and Sinclair2011). The most inferentially threatening sorts of homophily occurs if legislators establish relationships because of their tendency to vote together or terminate relationships because of their tendency to vote differently, as in the “unfriending” problem (Noel and Nyhan Reference Noel and Nyhan2011). Not all relationships form because of homophily, but the primary challenge to measuring social influence is specifying conditions under which the distribution of ties is ignorable.

Yet, there is also a third theoretical possibility that combines homophily and anticipated influence. Individuals may form ties with the explicit purpose of changing their own future behavior, in effect “choosing to be changed” (Santoro Reference Santoro2017). For example, a new member may seek out a senior colleague as a role model because of both perceived homogeneity and the intent to learn and thus change future behavior. This phenomenon blends elements of homophily and influence, implying that individuals not only select into relationships for nonrandom reasons but also subsequently change because of those relationships. Insofar as individuals bear the seeds of the change that follows, the process resembles homophily. Insofar as they were unlikely to change in the absence of the relationship, it is also unmistakably influential.

Cue-taking depends on qualities of social ties more generally. Ties vary in terms of strength—whether the relationship entails close, frequent, and durable interactions rather than casual, novel contact. Granovetter (Reference Granovetter1973) famously argues that the latter, “weaker” ties are actually the source of a network’s “strength.” While strong ties often develop in tightly knit groups, weak ties are more likely to bridge structural holes between different groups (Burt Reference Burt2009). Within tightly knit groups, information is shared quickly and exhaustively. In contrast, weak ties transmit more novel information. Scholars have documented the strength of weak ties between legislators, with consequences for legislative success (Kirkland Reference Kirkland2011), legislative effectiveness (Battaglini, Sciabolazza, and Patacchini Reference Battaglini, Sciabolazza and Patacchini2020), and information exchange (Ringe, Victor, and Gross Reference Ringe, Victor and Carman2013) in a variety of contexts (Wojcik Reference Wojcik2018). In the case of legislative cues, these weak ties should be better at transmitting easily audited information, such as party calls (Minozzi and Volden Reference Minozzi and Volden2013) or the positions of allies and opponents, than technical information that would fall prey to cheap talk-like impediments to information flow.

We identify both weak ties and “choosing to be changed” with certain relationships. First, ties between legislators should be weaker when the ties are newer and stronger when they have been repeated often. Second, when members enter a legislature for the first time, they may be more likely to form relationships with peers or senior colleagues whose traits they seek to emulate. During the boardinghouse era, the first decision made by many new members will have been where—and with whom—to live. The resulting relationships will be nascent and thus both relatively weak and chosen with the intent for future change.

To summarize, informal cue-taking should be more prominent under certain conditions. First, actors must have sustained contact. Second, actors must have limited capacity to curate relationships. Third, there must be relatively few competing sources of influence. Fourth, weaker ties should convey more information than stronger ties, and cue-taking should be more common for ties including new members who “choose to be changed.” In the next section, we use the historical record and secondary sources to argue that conditions for social influence were satisfied by the boardinghouse culture of Washington DC before the Civil War.

Elite Social Life in Early Washington

Before the Civil War, elite social life in Washington was marked by intense, sustained contact. Members were socially concentrated yet physically isolated from the rest of the country. In 1801, serving in Congress meant isolation from everything familiar and comforting: families, friends, and associates (Riley Reference Riley2014; Zagarri Reference Zagarri2013). Postal service was slow; a letter would take a week to travel from Washington to New England and even longer to the westernmost part of the country (Young Reference Young1966). Washington itself was exceptionally limited (Earman Reference Earman1992). At the dawn of the century, there were only about 400 buildings (Green Reference Green1962, 4ff.). Yet the city grew quickly. A complicated system of etiquette emerged (Cooley Reference Cooley1829), including the pivotal role of women in establishing informal social ties with new arrivals (Allgor Reference Allgor2002; Earman Reference Earman2000).

Practically speaking, joining Congress meant finding somewhere to live and eat. Limited choices meant that most members lacked fine control over the selection of housemates. Options included boardinghouses, hotels, and private residences, in order of increasing cost (Earman Reference Earman1992; Shelden Reference Shelden2013, 102ff.; Young Reference Young1966). Boardinghouses were the most common selection, with many located near Capitol Hill (Earman Reference Earman2000). They varied in size, expense, quality, and social composition. Coresidents typically shared meals with each other. In some, dining companions included military officers, professionals, and travelers; in others, legislators had separate dining rooms (Earman Reference Earman1992). All told, boardinghouse life featured sustained contact and frequent opportunities to interact with coresidents but incomplete control over selection.

These opportunities were literally illustrated by Rep. Amasa Parker (D-NY), who included a drawing of his boardinghouse, Mrs. Pittman’s, in a letter to his wife (December 31, 1837; see Figure 1). Seated at the dining table were representatives and senators, including future president Millard Fillmore. The dining room and parlor for legislators and their spouses were separate from those for other boarders, permitting members to talk politics over meals in privacy. The oval table encouraged conviviality, and the company and environment were conducive to informal socialization. This example highlights the limits—or disinclination—of at least some legislators to select coresidents. Parker’s messmates included members of both chambers and major parties, Northerners, and Southerners. Few such illustrations remain, but evidence suggests that Parker’s experience was not atypical (see, e.g., Shelden Reference Shelden2013).

Figure 1. A Map of Seating at Mrs. Pittman’s from a Letter from Rep. Amasa Parker to His Wife, December 31, 1837, 25th Congress

Note: Clockwise from the top, they are Rep. Hugh Anderson (D-ME), Rep. John Fairfield (D-ME), Rep. Heman Allen (W-VT), Rep. Hopkins Holsey (D-GA), Rep. Millard Fillmore (W-NY), Mrs. Fillmore, Rep. Zadock Pratt (D-NY), Mrs. Pratt, Mrs. Prentiss, Sen. Samuel Prentiss (W-VT), Rep. John H. Prentiss (D-NY), Mrs. Knight, Sen. Nehemiah Knight (W-RI), Mrs. Birdsall, Rep. Samuel Birdsall (D-NY), Rep. Robert McClelland (D-NY), Rep. Amasa Parker (D-NY), Rep. Albert White (W-IN), and Rep. Andrew Buchanan (D-PA). Finding aid retrieved from http://hdl.loc.gov/loc.mss/eadmss.ms008132.

Outside the boardinghouse, the ambient political environment included relatively few competing sources of information, especially early in the period. Parties were not solidly entrenched as institutions, leaders, and sources of influence until the 1830s, and partisan labels and attachments were not as meaningful as they later became (Aldrich Reference Aldrich2011). Sectional conflict often counteracted partisanship (Poole and Rosenthal Reference Poole and Rosenthal1997), and standing committees did not fully emerge until the 1820s (Gamm and Shepsle Reference Gamm and Shepsle1989). To the extent that presidents lobbied, they did so informally, over dinners and on social occasions.Footnote ² Outside interests were similarly undeveloped. Organized interests did not exist even in vestigial state until after Reconstruction (Jacob Reference Jacob2010; Thompson Reference Thompson1985; but see Peart Reference Peart2018), and newspapers were controlled by party entrepreneurs rather than independent interests (Carson and Hood Reference Carson and Hood2014; Pasley Reference Pasley2002).

Some boardinghouses developed distinct political reputations. For illustration, consider Carroll Row, sometimes called “Six Buildings” or “Duff Green’s Row,” on First Street between East Capitol and A Streets SE. Daniel Carroll built these row houses on speculation before the government relocated (Bryan Reference Bryan1904). Over the decades, tenants included boardinghouses, hotels, and businesses, including an apothecary and a pub. In 1834, the easternmost house of Carrol Row became Mrs. Sprigg’s boardinghouse, which quickly emerged as a haven for abolitionists, earning the name “Abolitionist House” (Winkle Reference Winkle2013, Chap. 2). Residents included ardent antislavery advocate Joshua Giddings of Ohio, legislative allies William Slade of Vermont and Seth Gates of New York, and journalists Theodore Dwight Weld and Joshua Leavitt, who were publicists for abolition. Although Mrs. Sprigg had once been a slaveholder, by then she was a quiet abettor of the Underground Railroad.

Mrs. Sprigg’s most famous resident was Abraham Lincoln, who lived there during his single term in Congress in 1847–8. This choice of lodging placed the future president in the midst of abolitionists and may have shaped his views on slavery (Paullin Reference Paullin1921). In 1847, Lincoln was one of three first-term representatives who chose to live at Mrs. Sprigg’s. The other two were Elisha Embree (W-IN), and P.W. Tompkins (W-MS), the lone Southerner in the house. All five other coresidents, including Giddings, were Whigs who had previously lived in the boardinghouse.Footnote ³ But not all would remain. By the second session, Embree and Tompkins had departed for different accommodations, Embree to a different boardinghouse, and Tompkins to Brown’s Hotel. The others—including Lincoln—all returned to Mrs. Sprigg’s. Given Lincoln’s later actions, this example is consistent with the possibility that he selected, chose to remain among, and may even have been influenced by his senior coresidents.

Congressional Residences, 1801–1861

To systematically analyze influence based on coresidence, we collected data from the 58 extant editions of the Congressional Directory from 1801 to 1861,Footnote ⁴ recording each member’s residence and where they “messed,” or took their meals, when available.Footnote ⁵ In all, we have residential and/or mess data for 11,775 legislator-residence-sessions.Footnote ⁶

For each member, we coded whether they lived in a Boardinghouse , Hotel , or Private residence based on contextual information. Many editions of the Directory specifically labeled private residences, hotels included the word “hotel” in their names, and most boardinghouses were named after their proprietors. In our initial pass, we categorized 88% of 3,589 residences. All but 65 of the remaining locations included only one resident, suggesting they were private residences; at least, they will not affect our analysis of coresidence. We resolved remaining ambiguities on a case-by-case basis, using other editions of the Directory. Footnote ⁷

We matched this information to data on legislators and votes.Footnote ⁸ Our unit of analysis is an undirected dyad of legislators in a session (n > 1.32 million). Our key causal variable is an indicator for Coresidence for a dyad.Footnote ⁹ To match residency information to voting records, we split roll-call votes into periods corresponding to editions of the Congressional Directory.

Our outcome measures focus on roll-call votes. Consistent with the literature, our primary outcome measure is voting Agreement , the fraction of votes on which members of a dyad voted similarly out of the number on which both voted. These scores are employed to measure similarity because they include information omitted by ideal point estimation (Masket Reference Masket2008). Since Agreement scores are logically impossible when comparing a legislator with a deceased colleague, we later rely on ideal point estimation, as described below.

To model coresident selection, we augmented these data with indicators for dyadic similarity in Party , State , or Region (North or South)Footnote ¹⁰ ; Occupation ; whether they were in their First Session or Returning from the most previous sessionFootnote ¹¹ ; service in the Military ; graduation from College ; Age ; and Seniority . Finally, absenteeism was common, reaching more than a third of votes in the 1840’s, perhaps because of the prevalence of alcohol (Shelden Reference Shelden2013). Therefore, we also track Coabsence , the fraction of votes for which neither voted or was present.Footnote ¹² Ultimately, we estimate the following regression model:

$$ \mathrm{\Pr}\left({\boldsymbol{Coresidence}}_{ij t}=1\right)={\mathrm{logit}}^{-1}\left({X}_{ij t}b+{W}_{ij}g+{Z}_{ij\left(t-1\right)}d+{a}_t\right), $$

where i and j index legislators, t indexes sessions, a_t refers to session-specific fixed effects, X_ijt to time-varying covariates, W_ij to time-invariant covariates, and Z_ij(t-1) to lagged covariates_.

Our data and analysis improve on previous studies in several ways. The quantitative evidence Young (Reference Young1966) presents is remarkable for its time, but limited to 116 roll-call votes from 1800 to 1821, largely serving to corroborate qualitative evidence. Bogue and Marlaire (Reference Bogue and Marlaire1975) use regression to analyze the 17th, 22nd, and 27th Congresses (1821–2, 1831–2, 1841–2), but they find no association between voting and coresidence. Parigi and Bergemann (Reference Parigi and Bergemann2016) analyze data from 1825 to 1841 using fixed-effects analysis, reporting a positive relationship between agreement and coresidence. In a second study, they focus on members who moved midterm, finding that they voted less often with their erstwhile colleagues. Each design relies on assumptions to identify effects, assuming that the forces that bring legislators together are independent of potential outcomes, no time-varying unobservables confound inference, or no dynamic relationships exist between coresidence and voting. As we shall see, all these assumptions are incorrect.

The Rise and Fall of Boardinghouse Culture

During the six decades before the Civil War, boardinghouse culture emerged, quickly became the dominant feature of social life, and then slowly declined (Figure 2). To anchor inferences, we split the period into five eras: the Jeffersonian (1801–17), Era of Good Feelings (1817–1825), Early Jacksonian before the Whig party emerged (1825–37), Late Jacksonian (1837–49), and Antebellum (1849–61). These breakpoints are useful but to some extent arbitrary, but all inferences are robust to small changes in definitions of eras.

Figure 2. Counts of Residences of Members of the House of Representatives (left panel) and Residents Themselves (right panel) by Year and Type of Residence

Note: Both panels reveal that boardinghouses were the dominant residence type for members, emerging early on. Yet by the Late Jacksonian (1837–1849) and into Antebellum era, boardinghouses fell out of favor, gradually being replaced by hotels.

When looking for shelter, legislators had many options (left panel, Figure 2). Boardinghouses were most common. At the peak in 1855, members collectively resided in 75 different boardinghouses. Boardinghouses were also the dominant selection (right panel). Of our nearly 12,000 cases, more than 77% chose a boardinghouse. In 12 sessions—about 20% of cases—more than 90% of legislators lived in one of these buildings. But by the end of this period, boardinghouse culture was moribund. As late as 1855, 57% of legislators still lived in boardinghouses, but that number declined to 26% by 1861. Simultaneously, the number of colleagues one could expect to live with had also dwindled. Between 1801 and 1846, a boardinghouse resident could expect to live with an average of 4 to 7 other legislators. By 1861, that number fell to 1.5. These trends reveal how the social role of the boardinghouse waned with the advent of the Civil War.Footnote ¹³

Who Lived with Whom, and Why?

With whom did legislators choose to live? To answer this question, we estimated logistic regressions of Coresidence . Given the over-time variation we show above, we fit separate models by era, with fixed effects at the period (i.e., congressional session) level. For inference, we bootstrap at the congressional session level, which is a common procedure used in networks, as dyads themselves are not exchangeable (see, e.g., Leifeld, Cranmer, and Desmarais Reference Leifeld, Cranmer and Desmarais2018).

Based on the logic of homophily, we hypothesized that similarity would explain who lived with whom. Indeed, Same Party , State , or Region all reliably predict who lived with whom (see Table 1).Footnote ¹⁴ These estimates are substantial and persistent. The estimates for Party , in particular, cohere with conventional wisdom. The strongest relationships appear during the first and second party systems, the Jeffersonian and Late Jacksonian. In the Jeffersonian era, legislators from the Same Party had a predicted probability of Coresidence that was 4.4 percentage points larger than that of noncopartisans (95% interval [3.8%, 5.6%]).Footnote ¹⁵ This difference is larger than it may seem. The overall rate of Coresidence in this era was only 3.9%, meaning copartisanship almost doubles the chances of living together. Other similarity measures also predicted Coresidence , albeit more sporadically. Overall, the models strongly suggest homophily in coresident selection.

Table 1. Logistic Regression Models of Coresidence

Note: The table presents the results of logistic regression models for each era. Standard errors are based on 1,000 bootstrap resamples over congressional sessions. Models also include indicators for each congressional session and for availability of covariates. *p < 0.05, ^** p < 0.01, ^*** p < 0.001.

More troubling for inference about influence, homophily also appears between Coresidence and Lagged Agreement . Through all eras, Lagged Agreement strongly predicts whether members lived together. In substantive terms, the estimates are smaller than those for Same Party . For example, in the Jeffersonian era, the average marginal difference in predicted probabilities for Lagged Agreement is 1.2% (see Figure 3, left panel). Despite this small size, the estimates are precisely estimated; all 95% intervals exclude zero. Thus, as with party and geography, there is clear evidence of homophily in voting and coresidence.

Figure 3. Average Marginal Effects of Lagged Agreement on the Probability of Coresidence in Percentage Points

Note: Bars depict 95% intervals based on bootstrapping over congressional sessions.

Whatever the reason for cohabitation, members who lived together were likely to repeat the arrangement. The strongest predictor of Coresidence is Lagged Coresidence . About 40% of cases of Lagged Coresidence were repeated, ranging from 38% to 44% across eras, revealing a potential problem. Legislators who usually disagreed may have sought alternative lodging, while those that agreed continued living together. Longitudinal designs can mistake the dissolution of ties for different levels of influence, conflating influence with the underlying causes of such “unfriending” (Noel and Nyhan Reference Noel and Nyhan2011). If dissimilarity explains moves, then comparing coresident dyads to noncoresident ones will overestimate influence. Fixed effects models assume away such dynamic relationships between treatment and outcome (Imai and Kim Reference Imai and Kim2019), so a complete picture requires analysis of repeated Coresidence .

Therefore, we analyzed dyads who lived together in the previous session, focusing on repeated Coresidence .Footnote ¹⁶ The results tell a different story from the full sample (see Table 2). The roles of State , Party , and Region are weaker, though intermittently predictive. In contrast, homophily based on similar voting not only remains important, but the relationship between agreement and coresidence is also more pronounced. The coefficients on Lagged Agreement are substantial and significant in the first four eras. Differences in predicted probabilities are about 10 times larger (Figure 3, right panel) than in the overall model, with an average increase of 7 percentage points. We conclude that legislators were likely to rely on political views not only to choose coresidents but also to choose whether to dissolve social relationships. As a consequence, fixed effects are inappropriate for identifying the effect of Coresidence on Agreement .

Table 2. Logistic Regression Models of Repeated Coresidence

Note: The table presents the results of logistic regression models for each era on the subsamples of dyads who were coresidents in the previous period. Sessions are excluded when no evidence exists for the relevant prior session. Standard errors are based on 1,000 bootstrap resamples over congressional sessions. Models also include indicators for each congressional session and for availability of covariates. *p<0.05, ^** p<0.01, ^*** p<0.001.

Dynamic Identification of Coresidence Effects

Given that Coresidence is predicted by previous voting Agreement , research designs such as fixed effects do not plausibly identify the effects of the former on the latter. An alternative identification strategy is to use inverse probability weighting (Blackwell and Glynn Reference Blackwell and Glynn2018) to explicitly account for dynamic relationships between treatment and outcome. This strategy relies on strong identifying assumptions, most notably sequential ignorability conditional on previous Coresidence and covariates, including Lagged Agreement . An important cost is that we no longer adjust for unobservable, time-invariant covariates, as with fixed effects. Although the cost is steep, our strategy is to offset it by pairing our aggregate analysis with a better-identified subsequent study based on legislator deaths, described below.

We used models with similar forms to those from above to estimate the probability of Coresidence , including fixed effects at the congressional session.Footnote ¹⁷ Because the selection processes for previously coresident and noncoresident dyads were different, we analyze these groups separately. For weights, we took predicted probabilities of Coresidence and assigned the inverse probability to coresident dyads and the inverse of its complement to noncoresident dyads.Footnote ¹⁸ Doing so substantially improved balance (see Appendix, A8–A9). Finally, we estimated weighted linear models of Agreement on Coresidence . For statistical inference, we bootstrapped at the congressional session level, resampling 1,000 times over sessions, testing the null hypothesis of zero average effect.

The results of our analysis appear in Figure 4. The black bars depict estimates of the effect of Coresidence on Agreement for dyads who did not live together in the previous session; the gray bars display the same for previous coresidents. In both cases, results are shown by era. Since Agreement ranges from 0 to 100%, results can be understood in terms of the percentage point increase in roll-call voting agreement due to Coresidence .Footnote ¹⁹

Figure 4. Estimated Effects of Coresidence on Agreement in Percentage Points

Note: Bars depict 95% intervals. Estimates are calculated using inverse probability of treatment weighting, with the block bootstrap over sessions.

In all cases, our estimates of the effects of Coresidence on Agreement are positive and, in the case of previous noncoresidents, statistically significant.Footnote ²⁰ The appendix presents several robustness checks, including a specification that adjusts for whether both members of a dyad chose to live in a boardinghouse and another in which we include fixed effects at the level of the individual legislator (see Appendix, A14–A15). In both cases, inferences are similar to those reported in the main text.

On balance, these findings suggest that social influence and cue-taking occurred regularly throughout the decades before the Civil War. On average, effect estimates were about 4.6 percentage points for dyads who lived apart in the previous session and about a third of that among pairs who previously lived together.Footnote ²¹

These results depart from previous work. Parigi and Bergemann (Reference Parigi and Bergemann2016) analyze the period from 1825–41, roughly equivalent to the Early Jacksonian era, using fixed effects to find estimates of 10 to 13 percentage points. For previous noncoresidents, we do see our largest estimated effect in that era—but our estimate is only half as large as is theirs. Given the evidence of homophily, this difference may be due to the improved research design.

We go beyond previous studies to test hypotheses about different sets of dyads. Based on the logic of “choosing to be changed” (Santoro Reference Santoro2017), we expected new members to have chosen coresidents with influence in mind and thus to have larger effects. Further, tie strength should increase with shared history. Based on the “strength of weak ties” (Granovetter Reference Granovetter1973), we expected effects to be small for previous noncoresidents who had lived together in the more distant past; smaller still for previous coresidents who lived together only once, in the most previous session; and smallest for previous coresidents who lived together more than once.

Figure 5 displays the conditional effects of Coresidence for each of these subgroups. In general, the results support both that new members may select into residences that are likely to influence them and that influence declines with tie strength. There is a clear, statistically significant difference between dyads with at least one new member and dyads with two returning members who had never lived together.Footnote ²² Moreover, there is a two-percentage-point difference between the estimate for those returning members who had never lived together and those for the strongest ties, legislators who had previously lived together (two-tailed p < 0.001).Footnote ²³

Figure 5. Estimated Effects of Coresidence on Agreement in Percentage Points

Note: Bars depict 95% intervals. The subgroups of dyads differ in terms of both tie strength and presence of a new member.

Once we adjust for the dynamic relationship between residence selection and voting behavior, there is robust evidence of social influence among legislators throughout the six decades prior to the Civil War. Our results further suggest that existing studies, which have focused on subsets of this period, have also overestimated these effects. Finally, our estimated effects are smallest in the years just before the Civil War, coincident with the decline in boardinghouse culture we documented above.

But our research design still relies on strong identifying assumptions, including that Coresidence is sequentially ignorable, conditional on covariates. This assumption has varying plausibility. For example, it is less plausible when we lack lagged Agreement scores, as with new members. We are reassured by the evidence of declining influence with increasing tie strength. Yet, despite the clear improvement in identification, this research design does not rival those that exploit randomization, such as Rogowski and Sinclair’s (Reference Rogowski and Sinclair2012) study of the office lottery. Next, we offer one last study to better approximate randomization.

Identifying Coresidence Effects with Legislator Deaths

We leverage occasions when a legislator died in office to identify the effect of his sudden absence on surviving coresidents.Footnote ^{24 ,} Footnote ²⁵ Using the Biographical Directory of the United States Congress, we identified legislators who died during congressional terms between 1801 to 1861. We include such legislators when they had at least one coresident. Further, to permit reliable measurement, we included only deceased legislators who cast at least 20 roll-call votes before their deaths and survivors who cast at least 20 votes before and 20 votes after. Ultimately, we identified 60 deceased legislators.Footnote ²⁶

These deceased legislators were representative of their population. Their deaths occurred throughout the period. The earliest was Rep. Charles Johnson (R-NC), who died on July 23, 1802; the latest, Rep. Silas Burroughs (R-NY), who died on August 3, 1860. The average deceased legislator resided in a boardinghouse, served two terms, and lived with about six coresidents. Twenty hailed from the South. More Virginians are included in the sample than denizens of any other state, but members of 20 delegations are included. The set includes Democrats, Federalists, Republicans (in both party systems), Whigs, and members of several third parties. The surviving coresidents are similarly representative.

Because legislators do not vote after their deaths, we cannot rely on Agreement scores. Therefore, we estimate changes in ideological distances between survivors and their deceased colleague before and after his death. If any legislator exerts influence on his coresidents, he would have had an attractive effect on the ideal points of his coresidents. After death, we should see those survivors move away from their erstwhile coresident’s ideal point, perhaps now more influenced by their own preferences, constituencies, parties, state delegations, or remaining or even new coresidents. The result should be that the distance between deceased legislator’s and survivors’ ideal points increases after death.

To estimate changes that occurred when a legislator died, we need separate measures for each survivor before and after his colleague’s death. Therefore, we used bridging (Poole Reference Poole2005, Chap. 6). First, for each deceased legislator, we built a dataset of votes and legislators. For legislators who died between sessions, we included the sessions immediately before and after the death; for those who died within a session, we restricted attention to that session. In both cases, we included the deceased legislator and all noncoresidents who served in the House both before and after the death date. We also included each survivor twice: once for votes before his colleague’s death and once for after. Noncoresidents are the bridges that identify distances between ideal points before and after death.Footnote ²⁷ We observed both before- and after-death ideal points for all surviving coresidents, so the attrition rate in this study is zero.

For each deceased legislator, we simulated two-dimensional ideal points using item response theory (Clinton, Jackman, and Rivers Reference Clinton, Jackman and Rivers2004).Footnote ²⁸ While multidimensional ideal point models suffer from nonidentification of several sorts, we are interested in distances between points rather than nominal values. Therefore, our measure is already invariant to rotation and translation. For nonidentification due to the scale of the policy space, we standardized each set of ideal points with respect to the bridge observations. Nevertheless, combining measures from different models means comparing sessions with different scales and thus the assumption that the policy space does not expand or contract. It is plausible, however, to make comparisons between different sets of ideal point distances in proportional terms using logs—effectively gauging the ratio by which the distances between legislators grew or shrank relative to the average distance between pairs of (bridge) legislators. Our outcome is therefore log Ideal Point Distance between a deceased legislator and surviving coresident, measured both before and after death.

To provide an effective contrast for residences in which legislators died, we used a similar strategy to estimate ideal point drift in residences that experienced no deaths.Footnote ²⁹ That is, for each of the remaining residences that housed more than one resident, we used the same technique as described above on each resident—essentially treating all residents from these residences as control cases—that is, nondecedents. We calculated the (log) distances before and after that legislator’s “death,” which we set at the break between sessions, to yield a comparable outcome variable. The result is a set of 28,362 (directed) dyads over 967 residence-terms.

Our analysis plan focuses on the changes in log Ideal Point Distance aggregated to the level of the residence.Footnote ³⁰ Thus, we regard each residence as either having been treated to a resident’s death or not. First, we calculate the change in log Ideal Point Distance after each legislator death or session break, based on treatment status. Second, we calculate the average of those changes at the level of the residence (so n = 60 residences with deaths + 967 residences without deaths = 1,027). Finally, we estimate a weighted least squares model of the mean change in log Ideal Point Distance , weighted by the number of dyads in each residence to track the amount of information provided by each observation. The main model specification is mean change in log Ideal Point Distance _rt = Resident Death _rt + a_t ,

where r indexes residences; t indexes congressional terms; Resident Death is the treatment variable, which is 1 if and only if a resident of residence r died within term t; and a_t represents fixed effects for era. This model emphasizes the focal role of the residence, though other designs are reasonable and yield similar results.Footnote ³¹ We also report on specifications including an indicator for Within Session , which indicates whether death occurred midsession (1) or between sessions (0); an indicator for Boardinghouse , which indicates whether a residence was a boardinghouse (1) or not (0); and a count of the Number of Legislator Residents in that residence-term.

Identification relies on one primary assumption. We assume that deaths occurred as though at random, so that each boardinghouse was equally likely to have experienced a legislator’s death.Footnote ³² While legislators died of many different causes (Maltzman, Sigelman, and Binder Reference Maltzman, Sigelman and Binder1996), we regard this assumption as at least facially plausible. For statistical inference, we use bootstrapped standard errors, resampling over residence-terms, with two-tailed p-values.Footnote ³³

Survivors Drift Away from Deceased Colleagues

As we hypothesized, surviving legislators drifted away from the ideological positions of their deceased colleagues. Overall, the estimated effect of Resident Death on mean change in log Ideal Point Distance was 0.072, with 95% interval [0.002, 0.140] and p = 0.04. Effects are interpretable in proportional terms, so this result means that a colleague’s death causes the distance between his ideal point and that of his deceased coresident to grow by about 7%, similar to the magnitude reported in the IPW study above.Footnote ³⁴

To vet the efficacy of this design, we deploy a placebo study, focusing exclusively on the 967 residences that did not experience a death, effectively treating residents of such residences as, alternately, “placebo decedents” and “placebo survivors,” with “placebo death” occurring at the break between sessions. Here, we randomly sample 60 residences—none of which experienced an actual death—and recode Resident Death to be equal to 1 only in those cases. We then use the weighted least squares procedure described above, bootstrapping for statistical inference.

We repeat this placebo test procedure 1,000 times to yield a distribution of placebo estimates and p-values.Footnote ³⁵ Given that none of the residences in this test experienced death, if the design is unbiased, we would expect to see (1) a flat, uniform distribution of placebo p-values and (2) that our estimated effect appears as an outlier in the distribution of placebo effects. Figure 6 confirms both of these expectations. Exactly 5% of placebo p-values were less than or equal to 0.05, and only 1.6% of placebo estimates were greater than or equal to the actual estimated effect of 0.072. We conclude that this design does not suffer from overrejection of the null or bias.

Figure 6. Results of 1,000 Simulated Placebo Tests Using All Residences That Did Not Experience a Death of a Resident

Note: Residences that did experience a death are excluded. The panel on the left displays a histogram of the (bootstrapped) p-values from these tests. The vertical dashed line indicates p = 0.05. The panel on the right displays a histogram of the estimated placebo effects, and the solid vertical line indicates the observed estimate of 0.072. Consistent with the design assumptions, only 5% of placebo p-values are less than or equal to 0.05, and only 1.6% of placebo estimates exceed the actual estimated effect.

We also examined several alternative models. First, we used the same design to estimate effects on mean change in (unlogged) Ideal Point Distance , which yields an estimated effect of Resident Death of 0.042 [–0.029, 0.109], in a similar direction to the effect for logged distance but not statistically significant. The result is therefore sensitive to transformation of the outcome variable. However, as we argued above, logging is more appropriate in this case, given that Ideal Point Distance is positive-valued, and that the ideal points are measured separately by congressional term. Second, we estimated a model including the multiplicative interaction of Resident Death and Boardinghouse , along with the constituent terms, expecting that deaths in boardinghouses would have larger effects due to the more close-knit ties such residences fostered. The interaction term was positive though imprecisely estimated, 0.068 [–0.072, 0.214]. However, the effect for boardinghouse residents is represented by the sum the coefficients on the interaction term and the main effect of Resident Death , and this quantity remains significant (0.970 [0.007, 0.186], p = 0.032). Similarly, we estimated two more interaction models, one with Within Session and a second with Number of Legislator Residents . In each case, the interaction terms were small and imprecisely estimated.

For robustness, we also estimated a version of this model at the dyad-level, rather than at the residence-level. Specifically, the model specification in this case is

log Ideal Point Distance _dt = After Death _dt + Resident Death _dt × After Death _dt +g_d ,

where d indexes dyads, t indexes congressional term, After Death indicates whether the outcome is measured before (0) or after (1) death/session break, and g_d is a dyad fixed effect. The main coefficient for Resident Death is subsumed by the fixed effects, and the quantity of interest is now the coefficient on the interaction term. The main model specification only differs by including fixed effects for era, which would also have been subsumed by the dyad fixed effects. If we omit era fixed effects from the main specification, the two models are identical. The estimates from the dyadic model are similar to those from the residence-level model, though the p-value increases slightly (0.060 [-0.007, 0.128], p = 0.078); see Appendix Table A11 (A20). Therefore, it appears that dyad-level analysis, and the concomitant omission of era-level fixed effects, decreases the point estimate, suggesting overtime variation consistent with that seen in the IPW study.

Finally, to judge whether extreme outliers are responsible for these results, we reestimated our residence-level main specification, replacing mean change in log Ideal Point Distance with median change, which is more robust to outliers. In this case, the point estimate is slightly higher, and the p-value decreases slightly (0.078 [0.007, 0.153], p = 0.034). Based on this model, it appears that, if anything, outliers may dampen the estimated effect.

We conclude from the analyses that the evidence from legislators’ deaths largely confirms that from the IPW study, both in terms of sign and magnitude, while noting that this result extends only to log distances and the associated changes in proportional terms.