MY557 Assessment:

Does extending the franchise increase left-party vote?

Evidence from the 2

ndReform Act

Candidate Number: 33762⇤

May 23, 2014

"The Conservative party, whose opinions have had my most sincere approval,have, to my mind, dealt themselves a fatal blow by the course which theyhave adopted."

Viscount Cranborne (later Prime Minister Lord Salisbury),House of Commons, 15th July 1867

1 Introduction

Suffrage expansions are generally held to lead to redistribution, largely because newlyenfranchised poorer voters are hypothesized to support left parties and redistributivepolicies. And indeed, the 1867 Reform Act was directly followed by the Liberals’ 1868election victory, lending prima facie support to this claim, and credence to Conservativeanti-reformists such as the Viscount Cranborne. However, Berlinski and Dewan (2011)have argued that Liberal victory was not caused by the Reform Act. This study usesa difference-in-differences approach to isolate the causal effect of the franchise expan-sion on the Liberal vote, as well as on party competition, by comparing constituencieswith different types of franchise rules. It finds that the franchise expansion did not in-crease Liberal party performance - if anything, it actually diminished it. However, itdid affect party competition; while expanding the franchise did not decrease the shareof constituencies with uncontested elections, it did increase the candidate-to-seat ratiooverall, so the existing competition grew stronger.

⇤Many thanks to Ben Ansell, Henry Thomson and Torun Dewan for data, and to Øyvind Skorge forLATEX code.

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2 Suffrage expansion and voting behavior

Existing theoretical work links suffrage expansions to an increase in redistributive policies(Meltzer and Richard, 1978; Boix, 2003; Acemoglu and Robinson, 2006), and this iscommonly assumed to work via vote choice; the newly enfranchised citizens vote forleft-wing parties, which in turn support redistributive policies. However, this mechanismhas found mixed empirical support. A cross-national study has found a robust positiveeffect of male enfranchisement on left-wing vote share (Morgan-Collins, 2013), which issupported in an analysis of the Italian case of 1912 (Larcinese, 2011) and the Norwegiancase of 1898 (Morgan-Collins, 2013).1 However, other work does not find a similar effect;in particular, Berlinski and Dewan’s (2011) analysis of the 1867 Reform Act in the UKfinds that expanding the vote was not associated with a particular increase of the Liberalparty’s vote share on a constituency level.2

2.1 The 2

ndReform Act

The 2nd Reform Act, which passed in August 1867, is a key example of such a franchiseexpansion. Called the "act that transformed England into a democracy" (Himmelfarb,1966: 107), it almost doubled the enfranchised population overall (Berlinski and Dewan,2011: 2) and has been argued to have had vast consequences for party competition(Berlinski and Dewan, 2011; Evans, 2000). It is also widely held to have precipitatedthe subsequent overwhelming 1868 Liberal election victory (e.g. Evans, 2000: 56), whichhas, in turn, been linked to increases in public goods spending (Lizzeri and Persico,2004: 753). In fact, many politicians themselves thought that an increase in the Liberalvote was likely (Bronner, forthcoming: 16); many Conservatives, in particular, werealarmed at the bill. However, while this initially seems like a clear case in support of thenotion that expanding the suffrage increased the left party’s vote and thereby broughtabout increased redistribution, empirical evidence on its effects so far has called this intoquestion. In particular, Berlinski and Dewan (2011) find that the increased electoratewas not associated with higher Liberal vote or seat shares on the constituency level, thuscalling into question the established wisdom. However, they do find that boroughs witha larger increase in registered voters did have a larger decrease in uncontested seats, anda larger increase in the candidate to seat ratio, than boroughs with fewer new voters;they thus argue that while the franchise expansion in the 2nd Reform Act cannot besaid to have caused the Liberals’ 1868 election victory, it did crucially increase partycompetition in the UK.

Their analysis is very valuable, particularly as they take advantage of the fact that theelectorate in boroughs changed differently to trace whether this difference was associated

1Moreover, studies examining the effect of introducing compulsory voting, which is also seen toincrease electoral turnout among lower-income voters, have also found a positive effect on left-wing voteshare (Bechtel et al., 2014; Fowler, 2013), which implies support for a similar causal mechanism.

2While the Liberal party is different from the socialist, social democratic and labour parties analysedby Morgan-Collins (2013) and Larcinese (2011), it was the left alternative to the Conservatives in the1860s and ‘70s.

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with a difference in the outcomes of interest. However, as they note themselves, theyobserve only a subset of the relevant population - those who registered to vote, ratherthan those who became eligible (Berlinski and Dewan, 2011: 4). This difference inregistration was due to registration officials, judges and other local factors.3 This makesit vulnerable to endogeneity, as omitted variables could be influencing both the increasein registered voters and the Liberal vote share. As just one example, a borough witha strong local Conservative presence (perhaps in the form of a particularly powerfullocal interest) may fear that newly enfranchised voters may support the Liberal party.4This strong Conservative interest may suppress local voter registration and result in alow Liberal party vote, so the theorized correlation would be at play, but the causalmechanisms would be quite different.5 This study, on the other hand, makes use of anexogenous treatment, which is whether the constituency in question is a borough or acounty. Rather than relying on the number of registered voters, it takes advantage of thevery different franchise rules the reform bill set out for borough and county constituenciesto develop a difference-in-differences design (see section 3).

3 Data and Method

3.1 Treatment

As noted above, the franchise was extended very differently in the two different types ofconstituencies. In the boroughs, the franchise was extended to all men over 21 residentfor at least 12 months, provided they either owned or rented a house (were ‘inhabitantoccupiers’), as well as to lodgers paying over £10/year. In the counties, however, it wasmuch more restrictive, being granted only to men who owned copyholds or had leases ofover 60 years worth over £5/year, and tenants renting land over £12/year (Evans, 2000:131-2; Berlinski and Dewan, 2011: 6). This difference, primarily the fact that the billenfranchised all homeowners and tenants as well as some lodgers in the boroughs, butonly some renters and rate-payers (and no lodgers) in the counties, was indeed reflected inthe way the electorate changed as a result of the reform; while there was variation in theimplementation, the franchise increased much more in the boroughs than in the counties

3For example, one amendment to the Reform Bill - the Hodgkinson amendment - abolished thepractice of compounding, in which occupiers of sub-units of a house paid rates via a landlord rather thandirectly. While this vastly increased the number of enfranchised voters by increasing the number whichpaid their rates directly, a condition of the franchise, this was not immediately clear in the aftemathof the bill’s passage, and initially local magistrates were responsible for deciding on individual cases,introducing variability.

4Elections in quite a few constituencies were almost entirely dominated by a locally notable individualor family (Mair, 1868), which would have made it very plausible for them to exert their influence overregistration as well, particularly as this was very unregulated centrally and left up to constituency officialsto implement (Berlinski and Dewan, 2011: 16).

5Berlinski and Dewan (2011: 21-2) are aware of this problem, and try to address it using an instru-mental variable (IV) appoach, instrumenting the increase in registered voters by using the 1832 electoratelevel and the 1861 population size, both of which are prior to the franchise reform and correlated withthe change in the electorate after the reform, which gives them similar results. However, they note thatthey cannot reject the overidentifying assumption at 10% confidence.

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- by 152%, compared to by 47% on average (Figure 1). The difference between counties’and boroughs’ franchise expansion can be expressed, in experimental terms, as ‘weak’and ‘strong’ treatment; both constituency types were subject to franchise expansion, butthe expansion in the boroughs was more inclusive on all counts, both in intention and ineffect (see Panel B of Figure 1).

It is crucial to note that boroughs and counties did not start out with the samefranchise rules - or the same proportion of enfranchised people. The pre-1867 franchisewas also more restrictive in the counties than in the boroughs; in the counties, mencould vote if they owned freehold property worth £2 or copyhold land worth £50/year,or rented land over £50/year. In the boroughs, on the other hand, all owners or occupiersof property worth over £10/year could vote if they had paid all taxes on the property anddid not receive poor relief, subject to an ownership requirement of 12 months (Evans,2000: 129). As the dotted lines in Panel B of Figure 1 show, in pre-reform boroughs(red) a slightly larger proportion of the population could vote compared to pre-reformcounties (blue). However, even though boroughs were starting from a more inclusivesituation, the reform itself still constituted a ‘strong’ treatment for them (compared tothe weak treatment in counties), as the change was relatively much larger in boroughsthan in counties, with regard to both the terms of the franchise rules and their effect;comparing the solid to the dotted lines in Panel B shows how much larger the increasein the proportion of the electorate was in boroughs, while Panel A shows the differenceas a proportion of the previous electorate. Moreover, a difference-in-differences designaccounts for this pre-reform variation, as section 3.3 explains.

3.2 Data

Data on constituency-level electoral statistics was provided by Torun Dewan, which is thesame as that used in Berlinski and Dewan (2011). In this paper, three key outcomes ofinterest are considered - firstly, the Liberal vote share, which is calculated quite simply asthe share of the vote obtained by Liberal candidates in a constituency; secondly, the shareof constituencies in which elections were uncontested, and finally, the ratio of candidatesto seats (which is 1 when the election is uncontested, and rises depending on the numberof candidates).

The 1867 Reform Act did not only expand the franchise, it also changed severalconstituency boundaries. In order to make sure that the pre- and post-reform units arecomparable, I follow Berlinski and Dewan (2011) in including only those constituencieswhich did not undergo a boundary change as part of the 1867 Reform Act.

Berlinski and Dewan (2011) also include Scottish constituencies, which were the sub-ject of the Scottish Reform Act which passed quickly following the Act for England andWales. However, while the franchise in Scotland followed the same general pattern asin England and Wales, there were some minor differences in the terms of both the pre-and the post-reform county franchises (Evans, 2000: 130, 132). For this reason, as a ro-bustness check I estimate the same models excluding Scottish constituencies (see section4.3).

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Figure 1: The change in electorate in boroughs and counties, 1865-8Figure amended from Berlinski and Dewan, 2011

3.3 Difference-in-differences

In an ideal situation, we would compare the same constituencies with a restricted and anexpanded franchise, in order to determine the causal effect of the expansion on Liberal

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vote share, uncontested elections and the candidate-to-seat ratio. However, two differentfranchises cannot be observed in the same constituency at the same time. I thus use adifference-in-differences design which allows me to estimate the causal effect of a moreinclusive franchise (Bechtel et al., 2014: 11).

The aim of the study is to estimate the causal effect of extending the franchise onthe electoral support of the Liberal party, on whether elections are uncontested, and onthe candidate-to-seat ratio; more precisely, it aims to estimate the effect of extending thefranchise more, as in the boroughs (‘strong treatment’) compared to extending it less, asin the counties (‘weak treatment’).

The units of the study are constituencies, i = {1, 2, ..., I0 � 1, I0, I0 + 1, ..., I}, inwhich voters voted in four elections, t = {1859, 1865, 1868, 1874}. Of these, 1859 and1865 took place before franchise reform, while 1868 and 1874 took place afterwards. Thisis expressed in the period indicator �, which is defined as

� =

⇢p if t = {1859, 1865}r if t = {1868, 1874} (1)

The causal effect of the ‘strong treatment’ effect compared to the ‘weak treatment’effect, or of being in a borough as opposed to a county, is

↵ATET = E [Yit(1)� Yit(0)|� = r, i I0] (2)

where Yit(1) is the potential outcome of constituency i and election t as a borough(strong treatment), while Yit(0) is the same constituency’s potential outcome as a county(weak treatment).

The causal effect of the more inclusive franchise on the boroughs (the ‘stronglytreated’), the ↵ATET , can be estimated using difference-in-differences based on the paral-lel trends assumption, which sets out that had the boroughs been given the weak (county)treatment, they would have behaved just like the counties did (Angrist and Pischke, 2009:230). This assumption can be formalized as

E [Yit(0)|� = p, i I0]� E [Yit(0)|� = r, i I0]= E [Yit(0)|� = p, i > I0]� E [Yit(0)|� = r, i > I0]

(3)

and means that we can estimate the effect of the more inclusive franchise restrictionfor the boroughs in the post-reform period by subtracting the observed difference betweenboroughs and counties before the reform from the observed difference afterwards:

↵ATET = E [Yit(1)� Yit(0)|� = r, i I0]= {E [Yit|� = r, i I0]� E [Yit|� = r, i > I0]}� {E [Yit|� = p, i I0]� E [Yit|� = p, i > I0]}

(4)

I estimate this difference-in-differences using regressions predicting the Liberal voteshare, the uncontested share, and the candidate-to-seat ratio, each delineated by Yit:

Yit = ↵ATETBroadFranchiseit + �i + �t + ✏it (5)

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Here, BroadFranchiseit is a binary variable (1 for boroughs in the treatment period,0 otherwise), and ↵ATET is the size of its effect. I also include constituency-level (�i)and election-level fixed effects (�t) to control for constituency-specific and time-specificunobserved factors (Angrist and Pischke, 2009: 229). ✏it is an error term.6 Includingthe fixed effects for both constituency and election year means that the estimate is notbiased by time-invariant constituency factors, such as basic economic, demographic oreven idiosyncratic characteristics, nor by general shocks.

The model is estimated using two-way clustered standard errors (Arai, 2008), whichhave no effect on the estimate size, but give more conservative standard errors (Bech-tel et al., 2014: 13; Angrist and Pischke, 2009: 224). This is in order to correct forintra-constituency and time-specific dependence; it is likely that the same constituency’selection results in different time periods will be correlated, as will national results in thesame election (due to general swings).

4 Results

4.1 Parallel trends

Before estimating the causal effect of the more inclusive franchise, it is necessary to seewhether one of the key assumptions underlying the difference-in-differences estimation,the parallel trends assumption, is plausible. While the assumption - which holds that hadthe boroughs been given the same treatment as the counties, they would have had thesame change in Liberal vote share, uncontestedness, or candidate ratio7 - is fundamentallyuntestable, as it involves a counterfactual, we can examine the trends in the two groupsprior to reform, in order to see whether these are similar.

Figure 2: Trends in the dependent variables6For estimating uncontestedness, which is a binary variable (an election is either contested or it is

not, regardless of the number of seats available), a logistic model with the same set-up was used.7See equation 3 in section 3.3.

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Table 1: The effects of franchise expansion

Liberal Vote % Uncontested? Candidate Ratio(1) (2) (3)

Broad Franchise -5.91 -0.4 0.14Twoway clustered SE (3.74) (0.45) (0.06)Twoway clustered p-value 0.12 0.37 0.03

No. of Observations 486 824 824No. of Constituencies 185 206 206Constituency FEs Yes Yes YesElection FEs Yes Yes Yes

Mean of Dep. Var. (treated) 60.42 0.32 1.6Effect size (% change) -8.91% -55.9% 9.43%

As Figure 2 shows, while for each of the three dependent variables there was a largedifference between counties and boroughs before the franchise extension in absolute terms,the two pre-reform elections (on the white background) indicate that the two constituencytypes were showing extremely similar trends from 1859 to 1865. This holds for all threedependent variables. Given this pre-reform similarity, the parallel trends assumption ismore plausible for the treatment period as well.

4.2 Difference-in-differences

Model 1 in Table 2 shows the effect of the strong treatment on the Liberal vote share,including constituency and election-year fixed effects, with twoway (constituency andelection-year) clustered standard errors and p-values. Somewhat surprisingly, the moreinclusive franchise extension appears to have a negative effect on the Liberal vote sharecompared to the less inclusive extension, though this estimate is statistically insignificant,like the small positive effect found by Berlinski and Dewan. It corroborates their findingthat expanding the franchise did not cause the 1868 Liberal election victory. (In fact,if anything, the more expansive increase in the boroughs may have hurt the Liberalsslightly.)

Similarly, model 2 shows that while the likelihood of a seat being uncontested diddecrease, and did so more in boroughs relative to counties; however, this decrease, likethe decrease in the Liberal vote share, is also insignificant. This contradicts Berlinskiand Dewan (2011), who find that boroughs with more newly enfranchised voters did havefewer uncontested elections than those with fewer new voters. A look back at the middleplot in Figure 2, which shows the general trends in uncontestedness for boroughs andcounties, shows that uncontestedness was less likely post-reform relative to pre-reform inboth types of constituencies; it does not appear that the stronger treatment in boroughsled to a significantly greater effect than in counties. However, while this suggests thatthe decline in uncontestedness was not caused by the franchise expansion, it does not

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Table 2: Robustness checks

Lib. Vote Lib. Vote Uncontested? Candidate Ratio(1) (2) (3) (4)

Broad Franchise -4.89 -4.81 -0.05 0.15Twoway clustered SE (4.32) (5.08) (0.64) (0.08)Twoway clustered p-value 0.26 0.34 0.94 0.07

No. of Observations 824 411 640 640No. of Constituencies 206 147 160 160Constituency FEs Yes Yes Yes YesElection FEs Yes Yes Yes YesIncluding Scotland Yes No No No

Mean of Dep. Var. (treated) 63.11 58.15 0.28 1.62Effect size (percent change) -7.19% -7.64% -14.55% 10.17%

rule out the possibility that the decline in uncontestedness was caused by the Act itself,such as by the increased public debate about representation, which may have galvanizedcandidates to run and voters to demand competition, but this is a different mechanismthan the franchise expansion itself, which does not appear to have been the cause.

The post-reform increase in the candidate-to-seat ratio, however, does appear tohave been driven by the extent of enfranchisement. While the ratio increased in all con-stituencies, it increased more in boroughs, which underwent the strong treatment, thanin counties, where the treatment was weak. The more inclusive enfranchisement resultedin a candidate-to-seat ratio an average of 9.4% higher than the less inclusive enfranchise-ment, a statistically and reasonably substantively significant effect. This suggests thatthe effect of the franchise expansion was subtle; it did not lead to competition startingin uncompetitive constituencies (where elections were uncontested), but it did increasecompetition in those areas where it was already taking place.

4.3 Robustness checks

Berlinski and Dewan’s estimations only predict the Liberal vote share when the electionwas contested; if the election was uncontested, the Liberal vote share is coded as missing.While model 1 in Table 1 follows this same logic, model 1 in Table 2 was estimated tomake sure that this decision was not affecting the results. Here, in uncontested elections,the Liberal vote share is set as equal to the share of seats that Liberals won (so in anuncontested election where a Liberal candidate stood for - and won - one of the twoavailable seats, the Liberal vote share is 50%). This inflates the number of observationsavailable, as fewer have missing values. However, this choice does not affect the results;as model 1 in Table 2 shows, the effect size is similarly negative but insignificant.

Another potential problem is the fact that the franchise rules in Scottish counties werevery slightly different to the rules in English counties (though boroughs were the same).

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Models 2-4 are, therefore, re-estimations of models 1-3 in Table 1, but excluding Scottishconstituencies, to make sure the results were not affected by this minor anomaly. Asthey show, this does not appear to have made a difference; the effects are very similar tothose including Scotland. The positive effect of the franchise extension on the candidate-to-seat ratio (model 4) is slightly less significant (p-value of 0.07 instead of 0.03), butlargely has the same magnitude and remains significant at 90% confidence.

4.4 Matching

Due to the fact that I do not have access to time-varying historical data on covariates,it is possible that my estimation is biased by time-varying factors that affect my strongand weak treatment units differently (see section 5). Though the time period underconsideration is fairly short (15 years), which reduces the likelihood that any of thesetime-varying factors will have had a major effect, the UK was in the process of industri-alizing at the time, which could have had an effect even within the period of the panel.Moreover, industrialization will have affected counties and boroughs very differently, asthey were rural and urban areas, respectively.

Figure 3: Histogram of counties and boroughs by propensity score

This robustness check thus compares the 1865 to 1868 change in the candidate-to-seatratio among counties and boroughs that were similar on key covariates: urbanization,agricultural workers as a percentage of the workforce (a proxy for industrialization), meanwage, Gini, and a measure of landholding inequality (Ansell, Samuels and Thomson, 2014:18). While, as noted, I do not have time-varying data on these covariates, I make anassumption that the level of key variables such as urbanization and industrialization isrelated to the rate of these processes. By matching on the level, I thus try and implicitlymatch on the rate of change, as well. This is a very flawed assumption, but if there is

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any truth at all to it then the matching exercise is useful as a robustness check to themain difference-in-differences result.

Figure 4: Pre- and post-matching balance of covariates betweencounties and boroughs

I use propensity score matching, which most closely approximates random matchingcompared to other matching strategies (King et al., 2011). In this method, covariates areused to predict the probability of a constituency falling into the treatment category (seeFigure 3), thus collapsing the covariate vectors into a scalar difference; constituencies arethen matched along this propensity for analysis. The covariates were selected in orderto reduce they the key observed differences between counties and boroughs: urbaniza-tion, mean wage, Gini, and the percentage of the workforce which is employed in theagricultural sector (see Figure 4 for pre- and post-matching balances). In this part ofthe analysis, due to the small number of counties without boundary changes for whichI had adequate covariate data, I set the county constituency as the ‘treated’ unit whilethe borough was treated as the control, such that I would be able to use all the countyobservations and match them with comparable borough observations. I used 1:5 match-

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Table 3: Predicting the change in the candidate-to-seat ratio using matching

County (weak treatment)

Estimate -0.24*Standard Error 0.11

No. of treated obs. 17No. of matched obs. 17No. of matched obs. (unweighted) 77***p < 0.001, **p < 0.01, *p < 0.05

ing with replacement, in order to increase the chances of an appropriate match. I thenpredicted the change in the ratio of candidates to seats from 1865 to 1868, using thepropensity score above.8 This gives an average treatment effect, ↵ATE , rather than anaverage treatment effect on the treated, ↵ATET (Angrist and Pischke, 2009: 69), so wedo not expect the effect size to be the same.

As Table 3 shows, even once constituencies are matched on four key economic covari-ates, counties have a significantly smaller change in the candidate-to-seat ratio between1865 and 1868 than boroughs do. This makes us more confident that the positive causaleffect of extending the franchise on the candidate-to-seat ratio, found in section 4.2, isgenuine.

5 Conclusion

While franchise expansion is generally held to lead to redistribution as it strengthensredistribution-oriented left parties, the 1867 Reform Act in the UK does not support thistheory. Rather, comparing boroughs, where the franchise was expanded very inclusively,to counties, where this was done much more conservatively, this study has shown thatthe Liberal party did not benefit electorally from this expansion; rather, if anything, thewider expansion appears to have diminished their performance slightly. Berlinski andDewan (2011) were thus right in pointing out that in contradiction to the much of theliterature, the 1868 Liberal election victory was not caused by the franchise extension.On the other hand, it would be wrong to claim that expanding the franchise had noeffect: it did increase party competition, a crucial facet of British political development.While it did not reduce the share of constituencies in which elections were uncontested,which decreased in all constituencies, it did make competitive elections more competitiveby increasing the candidate-to-seat ratio.

However, despite the fact that the difference-in-differences approach does allow usto make causal claims, the study still has limitations. One such limitation is that the

8By dropping the 1859 and 1874 elections, and predicting the change in the candidate-to-seat ratiobetween 1865 and 1868 rather than the level in 1868, I try to control for the different levels of thedependent variable in 1865.

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effects estimated here are not the effects of the treatment relative to the control, as inexperimental set-ups, but rather of a strong relative to a weak treatment. While thisensures that the estimates here are very conservative, it is highly likely that the trueeffect of franchise expansion (relative to the status quo) is underestimated. Thoughtaking this underestimation into account would not result in a positive effect of franchiseextension on the Liberal vote share (as the estimated effect is negative), but I am likelyunderestimating the effect of the franchise expansion on whether seats were uncontestedand on the candidate-to-seat ratio. While the latter was found to have decreased as aresult of the expansion, the former was not found to have changed significantly - whichmay be due to the underestimation of the treatment effect.

Another limitation is that as noted in section 4.4, this estimation strategy does notaccount for time-varying factors that affect counties and boroughs differently. As thiswas a time of vast economic change, driven by industrialization, which did indeed havedifferent effects in the towns and the countryside, this might be a concern.9 While Ihave tried to address this by matching counties and boroughs which were similar onkey covariates, I do not have time-varying data, and so this was based on the imperfectassumption that the level of industrialization and urbanization would be related to therate at which these processes take place. This does not address the problem of time-varying, constituency-varying trends as well as I would like, but it does help alleviateconcerns somewhat. However, the briefness of the period under consideration, only 15years between 1859 and 1874, does mean that we have less to worry about regardingpotential time-varying confounders - although this is a limitation itself, particularly asMorgan-Collins (2013) finds that the effects of enfranchisement on left-party vote sharegrow over time.

The final potential limitation is related to the sample; as the set of unchanged con-stituencies differed systematically from the changed ones, there may be a selection issue.In particular, as Berlinski and Dewan note, it is possible that Disraeli, the ConservativeChancellor of the Exchequer who largely orchestrated the passage of the Reform Actthrough the Commons, changed only those constituencies in which he anticipated theLiberals doing well, in order to improve the Conservative electoral performance (Berlin-ski and Dewan, 2011: 13). Comparing the Liberal share of the votes in 1865 shows thatLiberals did not do significantly better in boroughs without change than those which didundergo a boundary change (Table 4). However, Table 4 also shows that county con-stituencies which underwent a boundary change did have a substantially higher Liberalvote share than county constituencies without a boundary change, a difference which isstatistically significant at the 90% confidence level. Moreover, while the share of con-stituencies that were uncontested and the candidate-to-seat ratio was similar in changedand unchanged counties, they differed more substantially in changed and unchangedboroughs.

9This may also have affected the assumption of non-interference between units, as many people weremoving from the countryside into towns to find work in factories as the importance of manufacturingexpanded, though this is unlikely to have impacted the findings here.

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Table 4: Liberal vote share by whether constituency boundaries changed

Liberal Vote Prop. Uncontested Prop. Candidates Ratio

Boroughs: no boundary change 0.60 0.37 1.48Boroughs: boundary change 0.61 0.48 1.42Counties: no boundary change 0.42 0.68 1.24Counties: boundary change 0.50 0.66 1.25

Moreover, it is important to note that this study has measured the causal effect ofthe franchise expansion only, which differed by constituency type - it has not taken intoaccount any general effects the Reform Act might have had on public consciousness;it measures only the causal effect of the more inclusive enfranchisement itself. TheAct may still have led to the Liberals’ 1868 victory in other ways - it is, for example,possible that by getting the Conservatives to pass what was essentially a Liberal policy,the Liberals’ party brand was strengthened while the Tories were seen as weak (thoughDisraeli’s aim seems to have been to demonstrate the opposite, and his mastery of theCommons, by passing the bill that had been Gladstone’s downfall). Alternatively, thecontroversial nature of the Reform Act within the Conservative party - as noted above,it had major opponents, such as the Viscount Cranborne - may have negatively affectedparty cohesion and morale in its aftermath, which may also have contributed to the bad1868 performance. The research design, which measures only the causal effect of themore inclusive franchise extension, would not capture any of these indirect factors, whichwould affect both counties and boroughs.

6 Bibliography

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Berlinski, Samuel, and Torun Dewan. 2011. “The Political Consequences of FranchiseExtension: Evidence from the Second Reform Act.” Quarterly Journal of Political Sci-ence 6(3-4): 329-376.

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Morgan-Collins, Mona. 2013. “Universal Suffrage and the Rise of Socialist Parties inEurope: Evidence from Eleven European Countries”. Working Paper.

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