Candidate Promises, Citizens Knowledge and Vote-Buying Experimental Evidence from the Philippines A Pre-Analysis Plan for Phase I * Cesi Cruz † Phil Keefer ‡ Julien Labonne § May 2013 The document will be registered in the Hypothesis Registry of the Abdul Latif Jameel Poverty Action Lab (J-PAL). We will submit this document to the Hypothesis Registry today (May 12th, 2013), and we ask the Registry to publish it on or after September 1st, 2013. 1 Introduction How do voters respond to precise information about candidate promises? Does it lead candi- dates to alter how they target their electoral strategies? A growing literature demonstrates that the prospect of competitive elections may be insufficient to persuade politicians to pur- sue development-oriented policies. One strand of policy analysis and research blames this on poor information and vote-buying. If voters could be better informed and illegal vote-buying could be suppressed, politicians would do more to improve service provision, for example. Vote-buying can be seen as the outcome of a political equilibrium in which politicians have weak incentives to promise and deliver development-oriented policies. We implement a field experiment to test whether more and more credible information about candidate promises during mayoral elections in the Philippines changes this equilibrium and encourages candi- * We thank Marcel Fafchamps, Clement Imbert, Pablo Querubin, Simon Quinn and two anonymous reviewers for constructive comments. Pablo Querubin graciously shared his precinct-level data from the 2010 elections with us. We are grateful for excellent research assistance from Michael Davidson. † UC San Diego; email: [email protected]‡ World Bank; email: [email protected]§ Oxford University; email: [email protected]1
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Candidate Promises, Citizens Knowledge and Vote-Buying
Experimental Evidence from the Philippines
A Pre-Analysis Plan for Phase I ∗
Cesi Cruz† Phil Keefer ‡ Julien Labonne§
May 2013
The document will be registered in the Hypothesis Registry of the Abdul Latif Jameel
Poverty Action Lab (J-PAL). We will submit this document to the Hypothesis Registry today
(May 12th, 2013), and we ask the Registry to publish it on or after September 1st, 2013.
1 Introduction
How do voters respond to precise information about candidate promises? Does it lead candi-
dates to alter how they target their electoral strategies? A growing literature demonstrates
that the prospect of competitive elections may be insufficient to persuade politicians to pur-
sue development-oriented policies. One strand of policy analysis and research blames this on
poor information and vote-buying. If voters could be better informed and illegal vote-buying
could be suppressed, politicians would do more to improve service provision, for example.
Vote-buying can be seen as the outcome of a political equilibrium in which politicians have
weak incentives to promise and deliver development-oriented policies. We implement a field
experiment to test whether more and more credible information about candidate promises
during mayoral elections in the Philippines changes this equilibrium and encourages candi-∗We thank Marcel Fafchamps, Clement Imbert, Pablo Querubin, Simon Quinn and two anonymous reviewers
for constructive comments. Pablo Querubin graciously shared his precinct-level data from the 2010 electionswith us. We are grateful for excellent research assistance from Michael Davidson.†UC San Diego; email: [email protected]‡World Bank; email: [email protected]§Oxford University; email: [email protected]
1
dates and voters to focus less on vote-buying and more on service delivery and public good
provision.
This documents presents the empirical strategy that we will follow to test for the impacts
of an information campaign implemented in May 2013 by volunteers in the Parish Pastoral
Council for Responsible Voting (PPCRV), the election-monitoring arm of the Catholic Church
in the Philippines. It covers the first phase of data collection and analysis. In approximately
two years, additional data will be collected to test for impacts on the quality of service delivery
and another pre-analysis plan will be written at a later stage.
The remainder of this document is organized as follows. Section 2 provides an overview
of the intervention. Section 3 lists the hypotheses to be tested. Section 4 describes the data
and the estimation strategy that will be followed is presented in Section 5.
2 The Intervention
2.1 Treatment
This project proposes to test the efficacy of a randomized information campaign conducted by
the election-monitoring arm of the Catholic Church in advance of the May 13, 2013 elections
in the Philippines. The campaign will inform potential voters of the pledges candidates make
regarding how they plan to allocate their budget across sectors if they are elected.
The treatment will consist of two parts. First, members of the PPCRV intervention team
will meet with candidates for mayor in all intervention municipalities, using the Commission
on Elections (COMELEC)’s official list of candidates. Each candidate will be asked (i) how
they intend to allocate the Local Development Fund across 10 sectors, (ii) to list specific
projects or programs that they intend to implement with the first two years of their term
and, (iii) specific goals and targets they intend to reach. We will tell candidates that PPCRV
will record and disseminate these campaign promises. The field teams will solicit responses
from all candidates, but candidates are free to decline to participate if they prefer.
Second, municipality-specific flyers will be prepared and potential voters in randomly
selected villages will be informed about the proposed sectoral allocations if elected. PPCRV
volunteers will distribute flyers through door-to-door visits to all households in the treatment
villages. Given that most of the money for vote buying is spent 1 to 2 days before the
2
election, the campaign will be rolled out a few days before the election. While it is likely
that candidates will know which barangays (villages) have been targeted by the information
campaign, we will notify them after the flyers have been distributed.
2.2 Power Calculations
We carried out power calculations through simulations (Arnold, Hogan, Colford and Hubbard
2011). We used available survey data on vote buying in Isabela, a Philippine province, to
estimate the mean of the variable of interest and the structure of the error, accounting for
clustering both at the village and municipal-level. In addition, we used data from similar
experiments in other countries to estimate our expected impacts. Specifically, we assumed a
7.5 percentage-point reduction in the prevalence of vote-buying. We then varied the number
of intervention municipalities, village per municipalities and households to be interviewed
in each village and ran 1,000 simulations for each triplet. In each simulation, we randomly
generated vote buying data with the above distribution and randomly allocated some villages
to treatment and control, assuming a 7.5 percentage-point reduction in vote-buying. In each
case, we ran a regression and recorded whether the null of no effect was rejected. Results
from the simulations indicate that a design with 20 interventions municipalities, 20 villages
per municipality (10 treatment and 10 control) and 5 households interviewed per barangay,
for a total sample size of 3,200, rejected the null of no effect 89 percent of the time; which we
interpret as having strong power.
2.3 Allocation to Treatment
Municipalities where the intervention will be implemented are drawn from two provinces,
selected for convenience, in Region I: Ilocos Sur (767 barangay, 32 municipalities and 2 cities)
and Ilocos Norte (557 barangay, 21 municipalities and 2 cities). We further restricted the
universe to municipalities with at least 2 candidates in the 2013 mayoral elections and at
least 10 barangays. This left us with a total of 23 municipalities, including 7 with significant
security concerns or uncooperative candidates. The intervention will be implemented in the
remaining 15 municipalities.
We now describe how, within each intervention municipality, we allocate villages to treat-
ment using a pairwise matching algorithm. First, for all potential pairs, the Mahalanobis
3
distance was computed using village-level data on population, number of registered voters,
the number of precincts, a rural dummy, turnout in the 2010 municipal election and incumbent
vote share in the 2010 elections).
Second, the partition that minimized the total sum of Mahalanobis distance between
villages in the same pairs was selected. Third, within each pair, a village was randomly
selected to be allocated to treatment; the other one serving as control group. The final
sample includes 176 treatment and 176 control villages in 15 municipalities (cf. Table A2-1).
3 Hypotheses
We aim to test five sets of hypotheses, relating to the short-term impacts of the intervention.
In addition, it is expected that the information campaign will have impacts on the quality of
service delivery and we aim to collect additional data in a couple of years to test for those
effects. As indicated above, another pre-analysis plan will be written for that part of the
experiment at a later stage.
Hypothesis 1 As a result of the intervention, citizens are more knowledgeable about candi-
dates in the mayoral elections and their campaign promises.
This first hypothesis will allow us to test whether the information provided as part of
the campaign was processed by citizens. Consistent with models of rational inattention, it is
likely that the effect will be stronger for information about sectors that the respondents care
more about.
Hypothesis 2 As a result of the intervention, sectoral allocations are more salient in citi-
zens’ overall assessment of candidates.
Hypothesis 3 As a result of the intervention, citizens are more likely to prefer candidates
whose recorded preferences are closer to their own.
Hypothesis 4 By decreasing uncertainty regarding the candidates’ positions, the intervention
leads to an increase in turnout, especially for voters with strong relative preferences for one
of the candidates.1
1This is related to findings by Leon (2013) in Peru.
4
Hypothesis 5 The intervention leads to a decline in the prevalence of vote-buying.
If the intervention improves candidates’ ability to make credible post-electoral promises
to citizens, it should reduce their incentives to make pre-electoral transfers to mobilize citizen
support.
4 Data
4.1 Data from COMELEC
Precinct-level data on turnout and vote share for all candidates for the 2013 elections will be
obtained from COMELECs website. We already have the data for the 2010 elections.
4.2 Household Survey
A standard household survey will be implemented in 352 villages in 15 municipalities. In each
village, 5 randomly selected households will be interviewed.2 The survey is expected to be
implemented in June 2013.
Political Knowledge. For each of the 10 sectors, respondents will be asked to name the
candidate with the highest proposed allocation. Following Kling, Liebman and Katz (2007),
we will create an index aggregating the various indicators on knowledge about the campaign
promises by taking the equally weighted average of the demeaned indicators (divided by
the control group standard deviation).3 So if Kis is individual i knowledge about sector s
promises, then the index knowledge is:
Ki =110
∑s
Kis − 1n
∑iKis
V ar(Kis|Ti = 0)
In addition, we will also collect data on political knowledge more generally; candidate
characteristics not provided as part of the intervention (past experience in elected office
and education levels) and knowledge of officials elected to provincial and national positions
(governor, congressman and vice-president). As above, we will create an index aggregating2Due to cost savings in implementing the campaign, we might be able to increase sample size in each village.3For individuals with at least one non-missing value we will impute the mean of the random assignment
group (Kling et al. 2007).
5
the various indicators by taking the equally weighted average of the demeaned indicators
(divided by the control group standard deviation).4
Salience. We will ask respondent the degree (on a five point scale) of salience for a a
number of issues and candidate characteristics. We will ask how important (i) proposed
sectoral allocations, (ii) gifts or money offered by the candidates, (iii) preferences of friends
and family, (iv) candidates’s ability to use political connections to get money and projects for
the municipality, (v) fear of reprisal and, (v) approachability or helpfulness of the candidates
are when deciding who to vote for.
Preferences over candidates. We will ask respondent the degree (on a five point scale)
to which they agree with each of the candidate’s promises. In addition, for individuals who
reported voting in the past election, we will collect data on vote choice. In order to reduce
over-reporting votes in support of the winner, we use a secret ballot. Respondents will be
given ballots with only ID codes corresponding to their survey instrument. The ballots will
contain the names and party of the mayoral candidates in the municipality, in the same order
and spelling as they appear on the actual ballot. The respondents will be instructed to select
the candidate that they voted for, place the ballot in the envelope, and seal the envelope.
Enumerators will not be able to see the contents of these envelopes at any point. Respondents
will be told that these envelopes will remain sealed until they are brought to the survey firm
to be encoded with the rest of the database.
Preferences over spending priorities. We will collect data on respondents’ preferences
regarding sectoral allocations. Similarly to what was asked from candidates, we will provide
respondents with 20 tokens, each representing 5% of the local development fund, that they
will allocate across the 10 sectors. We will use this information to create an index of overlap
between the respondent’s preferences and the candidates’ preferences. More specifically, if
Svs is the share that voter v would spend on sector s and Scs is the share that candidate c
proposes to spend on sector s, then our index of agreement will be defined as:4For individuals with at least one non-missing value we will impute the mean of the random assignment
group (Kling et al. 2007).
6
Avc =∑
s
min(Svs, Scs)
Put differently, Avc is the share of total spending over which candidate c and voter v
agree.
Occurrence of vote-buying. The survey will use different techniques to collect data on
the prevalence of vote-buying in the 2013 elections. First, we will use an unmatched count
technique. The technique presents respondents with a set of statements that could have
potentially happened to them during the elections. Respondents are asked only to report the
number of items that happened to them, and not which items happened to them. Respondents
are assigned randomly to two sets of items. The first one receives a set of control statements
that are largely neutral and infrequent, while the second one receives the same set of control
statements, plus the additional statement: “Someone offered me money or gifts for my vote.”
Because the groups are randomly assigned, the prevalence of vote buying can be estimated
by comparing the means of the treatment and control groups. This is based on the rationale
that any additional increase in the average number of items reported can be attributed to
vote buying. The unmatched count method provides a non-invasive way to obtain accurate
estimates of vote-buying within individual villages. The anonymity this method provides does
not allow us to know whether specific individuals sold their vote, but it provides an accurate
village-level estimate of vote-buying.
More specifically, if C1iv is the count for individual i in village vthat was offered the first
set of items (sample size Ni) and C2jv is the count for individual j in village v that was offered
the second set of items (sample size Nj). Our measure of vote-buying in village v is
Vv =1Nj
∑j
C2jv −
1Ni
∑i
C1iv
Second, we intend to ask a series of direct questions: Did vote-buying occur in their
barangay? Was the respondent offered money or gifts in exchange for their vote? If so,
when? Did the respondent accept the money or gifts? Did the respondent vote for the
candidate? We will also ask about attitudes towards vote-buying.
Preliminary analysis of survey data from Isabela, another province in the Philippines
7
where vote-buying is rampant, suggests that both techniques generate credible measures of
vote-buying. The use of both techniques can increase the credibility of our results.
Additional variables. We will also collect data on: group membership, participation in
bayanihan (a measure of collective action), participation in barangay assemblies, number of
relatives involved in politics, religious denomination, income, asset and access to information.
5 Methodology
5.1 Test for Balance
We will first test for balance along pre-intervention characteristics between treatment and
control villages, including the six variables that we used to do the pairwise matching and
variables collected in the endline survey (preferences over sectoral allocations,5 household
composition, education levels of the respondent in years, gender of the respondent, group
membership, participation in bayanihan, participation in barangay assemblies, number of
relatives involved in politics, religious denomination, income, asset and access to information).
Specifically, we will run t-tests of equality of means and Kolmogorov-Smirnov tests of equality
of distribution. We will regress each of the variable on a dummy equal to one if the campaign
was implemented in the village and on a set of pair dummies.6
See Table A1-1 for a template and for initial results for the variables that were used to do
the pairwise matching.
5.2 Estimation Strategy
In this section, we list the regressions that we will run once the data are available. All
results will be reported in the paper. We anticipate running additional regressions during the
data analysis stage, in order to explore further the relationships that emerge from running
our registered regressions. If so, the associated results will be labelled as such in the paper
(Casey, Glennerster and Miguel 2012).5There is a risk that if voters have strong pre-intervention preferences over a candidate they might align
their preferences with the candidate’ promises. In that case, the sample might not be balanced along thosevariables. If that is the case, we will test if the distance between voter preferences and promises of theirpreferred candidate are smaller in treatment barangays than in control barangays.
6We will not necessarily control for control for variables that show a statistically significant difference inmean pre-treatment (Brunh and McKenzie 2009).
8
5.2.1 Hypothesis 1
Hypothesis 1 will be tested using individual-level data on knowledge about candidates and
their platforms. First, we will estimate the intervention’s impacts on knowledge of candidates’
promises:
Yijk = αTj + vk + uijk (1)
where Yijk is the knowledge index for individual i in village j in pair k, Tj is a dummy
equal to one if the campaign was implemented in village j, vk is a pair-specific unobservable
and, uijk is the usual idiosyncratic error term. To account for the way the randomization was
carried out standard errors will be clustered at the village level.
We will estimate equation (1) without fixed-effects, with municipal fixed effects and with
pair fixed effects (Brunh and McKenzie 2009). In addition, we will test if results are robust to
the inclusion of a number of control variables. See Table A1-2 for a template. Our preferred
specification will be the one with pair fixed effects and without additional controls.
Second, consistent with models of rational inattention, it is possible that voters will only
process information about the sectors they care most about. To test for that, we will regress
sector-specific measures of information about candidate promises, interacting the treatment
dummy with the share of budget respondents would allocate to the sector. Specifically, we
will estimate:
Yijs = αSis + βSis ∗ Tj + ws + vi + uijs (2)
where Yijs captures information individual i in village j has about candidates’ promises
on sector s, Tj is a dummy equal to one if the campaign was implemented in village j, Sis
is the share of LDF spending that individual i would want to allocate to sector s, ws is a
sector-specific unobservable and vi is a respondent-specific unobservable and uijs is the usual
idiosyncratic error term. To account for the way the randomization was carried out standard
errors will be clustered at the village level.
We will estimate equation (6) without fixed-effects, with municipal fixed effects, with pair
fixed effects and with individual fixed-effects. See Table A1-3 for a template. Our preferred
specification will be the one with individual fixed effects.
9
Third, it is possible that voters will only process the information when the differences
between the candidates’ promises are large enough. To test for that, we will regress sector-
specific measures of information about candidate promises, interacting the treatment dummy
with the gap between the top two promises in each sector. Specifically, we will estimate:
Yijs = αGjs + βGjs ∗ Tj + ws + vi + uijs (3)
where Yijs captures information individual i in village j has about candidates’ promises
on sector s, Tj is a dummy equal to one if the campaign was implemented in village j, Gjs
is the gap between the top two promises in sector s in municipality j, ws is a sector-specific
unobservable and vi is a respondent-specific unobservable and uijs is the usual idiosyncratic
error term. To account for the way the randomization was carried out standard errors will
be clustered at the village level.
We will estimate equation (3) without fixed-effects, with municipal fixed effects, with pair
fixed effects and with individual fixed-effects. See Table A1-4 for a template. Our preferred
specification will be the one with individual fixed effects.
Finally, to test if, as a result of the campaign, citizens are more interested in politics, we
will estimate the intervention’s impacts on political knowledge (not provided as part of the
campaign):
Yijk = αTj + vk + uijk (4)
where Yijk is the knowledge index for individual i in village j in pair k, Tj is a dummy
equal to one if the campaign was implemented in village j, vk is a pair-specific unobservable
and, uijk is the usual idiosyncratic error term. To account for the way the randomization was
carried out standard errors will be clustered at the village level.
We will estimate equation (4) without fixed-effects, with municipal fixed effects and with
pair fixed effects (Brunh and McKenzie 2009). In addition, we will test if results are robust to
the inclusion of a number of control variables. See Table A1-2 for a template. Our preferred
specification will be the one with pair fixed effects and without additional controls.
10
5.2.2 Hypothesis 2
Hypothesis 2 will be tested using individual-level data on how salient sectoral allocations are.
Specifically, we will estimate:
Yijk = αTj + vk + uijk (5)
where Yijk captures how salient sectoral allocations are when individual i in village j in
pair k decides which candidate to vote for, Tj is a dummy equal to one if the campaign was
implemented in village j, vk is a pair-specific unobservable and uijk is the usual idiosyncratic
error term. To account for the way the randomization was carried out standard errors will
be clustered at the village level.
As above, we will estimate equation (5) without fixed-effects, with municipal fixed effects
and with pair fixed effects (Brunh and McKenzie 2009). In addition, we will test if results
are robust to the inclusion of a number of household-level control variables. See Table A1-2
for a template. Our preferred specification will be the one with pair fixed effects and without
additional controls.
5.2.3 Hypothesis 3
Hypothesis 3 will be tested using individual-level data from the endline survey and precinct-
level data on candidate vote share. First, we will use individual-level data on support for the
various candidates’ promises and alignment between respondents’ preferences over spending
and candidates’ promises. Specifically, we will estimate:
Yijc = αAic + βTj ∗Aic + wc + vi + uijk (6)
where Yijc is a measure of the strength of individual i’s support for candidate c, Tj is
a dummy equal to one if the campaign was implemented in village j, Aic is the alignment
of individual i and candidate c preferences defined in Section 4.2, wc is a candidate-specific
unobservable, vi is a respondent-specific unobservable and uijc is the usual idiosyncratic error
term. To account for the way the randomization was carried out standard errors will be
clustered at the village level.
We will estimate equation (6) without fixed-effects, with municipal fixed effects, with pair
11
fixed effects and with individual fixed-effects. See Table A1-5 for a template. Our preferred
specification will be the one with pair fixed effects and without additional controls.
Second, we will use precinct-level data on candidate’s vote share in the 2013 elections.
(0.325) (0.311) [0.738] [1.000] [0.707]Panel B: Data from the household surveyIndicator
() () [] [] []
Notes: n=352 (Panel A). The standard deviations are in (parentheses) (Columns 1-2). In Columns3-4, the test statistics are reported along with the p-values [bracket]. Each cell in Column 5 is eitherthe coefficient on the dummy variable indicating whether the campaign was implemented in the villagefrom a different OLS regression with pair fixed-effects or the associated p-value in [bracket].
17
Table A1-2: Results from estimation of equations (1), (4) and (5)(1) (2) (3) (4)
Treatment() () () ()
Municipal Fixed-Effects No Yes No NoPair Fixed-Effects No No Yes YesAdditional controls No No No Yes
ObservationsR-squared
Notes: Results from individual-level OLS regressions. The standard errors (in parentheses) are Huber-corrected and account for intra-village correlation. * denotes significance at the 10%, ** at the 5%and, *** at the 1% level.
Table A1-3: Results from estimation of equation (2)(1) (2) (3) (4)
Treatment -() () () -
Sectoral Importance() () () ()
Interaction() () () ()
Municipal Fixed-Effects No Yes No NoPair Fixed-Effects No No Yes YesIndividual Fixed-Effects No No No Yes
ObservationsR-squared
Notes: Results from sector*individual-level OLS regressions. All regressions also include sector fixedeffects. The standard errors (in parentheses) are Huber-corrected and account for intra-village corre-lation. * denotes significance at the 10%, ** at the 5% and, *** at the 1% level.
18
Table A1-4: Results from estimation of equation (3)(1) (2) (3) (4)
Treatment -() () () -
Sectoral Difference() () () ()
Interaction() () () ()
Municipal Fixed-Effects No Yes No NoPair Fixed-Effects No No Yes YesIndividual Fixed-Effects No No No Yes
ObservationsR-squared
Notes: Results from sector*individual-level OLS regressions. All regressions also include sector fixedeffects. The standard errors (in parentheses) are Huber-corrected and account for intra-village corre-lation. * denotes significance at the 10%, ** at the 5% and, *** at the 1% level.
Table A1-5: Results from estimation of equation (6)(1) (2) (3) (4)
Treatment -() () () -
Policy Alignment() () () ()
Interaction() () () ()
Municipal Fixed-Effects No Yes No NoPair Fixed-Effects No No Yes YesIndividual Fixed-Effects No No No Yes
ObservationsR-squared
Notes: Results from candidate*individual-level OLS regressions. All regressions also include candidatefixed effects. The standard errors (in parentheses) are Huber-corrected and account for intra-villagecorrelation. * denotes significance at the 10%, ** at the 5% and, *** at the 1% level.
19
Table A1-6: Results from estimation of equation (7)(1) (2) (3) (4)
Treatment() () () ()
Policy Alignment() () () ()
Interaction() () () ()
Municipal Fixed-Effects No Yes No NoCandidate Fixed-Effects No No Yes NoPair Fixed-Effects No No No Yes
ObservationsR-squared
Notes: Results from candidate* precinct-level regressions. The standard errors (in parentheses) areHuber-corrected and account for intra-village correlation. * denotes significance at the 10%, ** at the5% and, *** at the 1% level.
Table A1-7: Results from estimation of equation (8)(1) (2) (3) (4)
Treatment -() () () -
Relative Preference() () () ()
Interaction() () () ()
Municipal Fixed-Effects No Yes No NoPair Fixed-Effects No No Yes YesVillage Fixed Effects No No No Yes
ObservationsR-squared
Notes: Results from individual-level OLS regressions. The standard errors (in parentheses) are Huber-corrected and account for intra-village correlation. * denotes significance at the 10%, ** at the 5%and, *** at the 1% level.
20
Table A1-8: Results from estimation of equation (9)(1) (2) (3) (4)
Treatment -() () () -
Relative Preference() () () ()
Interaction() () () ()
Municipal Fixed-Effects No Yes No NoPair Fixed-Effects No No Yes YesAdditional Controls No No No Yes
ObservationsR-squared
Notes: Results from precinct-level regressions. The standard errors (in parentheses) are Huber-corrected and account for intra-village correlation. * denotes significance at the 10%, ** at the 5%and, *** at the 1% level.
Table A1-9: Results from estimation of equation (10)(1) (2) (3) (4)
Treatment() () () ()
Municipal Fixed-Effects No Yes No NoPair Fixed-Effects No No Yes YesAdditional controls No No No Yes
ObservationsR-squared
Notes: Results from village-level OLS regressions. Robust standard errors (in parentheses). * denotessignificance at the 10%, ** at the 5% and, *** at the 1% level.
Annex 2: List of Intervention Municipalities
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Table A2-1: List of municipalitiesProvince Municipality # Pairs # CandidatesILOCOS NORTE BANGUI 7 2