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Military Culture and Institutional Trust: Evidence from Conscription Reforms in Europe

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Abstract

Does military conscription reduce the distance between the ordinary citizen and the state? Decades after its abolition, numerous European policymakers from across the political spectrum advocate the reintroduction of conscription to foster civic virtues, despite a lack of empirical evidence in this respect. Leveraging quasi-random variation in conscription reforms across 15 European countries, we find that cohorts of men drafted just before its abolition display significantly and substantially lower institutional trust than cohorts of men who were just exempted. At the same time, ending conscription had no effect on institutional trust among women from comparable cohorts. Results are neither driven by more favourable attitudes towards the government, nor by educational choices. Instead, this civil-military gap unfolds through the formation of a homogeneous community with uniform values. We argue that reintroducing a compulsory military service may not produce the e ects anticipated by its advocates.
Military Culture and Institutional Trust: Evidence from
Conscription Reforms in Europe
Vincenzo BoveRiccardo Di LeoMarco Giani
Forthcoming in American Journal of Political Science
Abstract
Does military conscription reduce the distance between the ordinary citizen and the state?
Decades after its abolition, numerous European policymakers from across the political spectrum
advocate the reintroduction of conscription to foster civic virtues, despite a lack of empirical
evidence in this respect. Leveraging quasi-random variation in conscription reforms across
15 European countries, we nd that cohorts of men drafted just before its abolition display
signicantly and substantially lower institutional trust than cohorts of men who were just
exempted. At the same time, ending conscription had no eect on institutional trust among
women from comparable cohorts. Results are neither driven by more favourable attitudes
towards the government, nor by educational choices. Instead, this civil-military gap unfolds
through the formation of a homogeneous community with uniform values. We argue that
reintroducing a compulsory military service may not produce the eects anticipated by its
advocates.
Keywords
: Military conscription; institutional trust; civil-military gap; Regression Discontinuity
(RD) design
Department of Politics and International Studies, University of Warwick.
Department of Economics, University of Warwick.
Department of Political Economy, King’s College London.
1
Introduction
As the collapse of the Soviet Union and the emergence of international terrorism deterritorialized the
military threat from the continent, a majority of European countries replaced obsolete conscripted
armies with highly technological, all-volunteer forces. Yet, as the debate around the merits of
such policy change seemed settled, an increasing number of policymakers from across the political
spectrum begun to advocate a U-turn on military labour policies. Discontinuing universal military
conscription, they claim, has contributed to widening the distance between the ordinary citizen
and the state. Several French commentators and politicians have, for example, lamented the loss
of the integrative and didactic function of the service national. “Historically, military conscription
was a mean for the state to pass on the Nation’s values”, claimed French sociologist Sébastien
Jakubowski, so that “(...) to end the military service was to tell young citizens that the Nation doesn’t
need them.
1
Senior gures in the French socialist party explicitly included the return of universal
conscription in their platform for the 2017 party primaries.
2
In the debate that followed, Emmanuel
Macron vowed to reinstitute a “service militaire universel” during the 2017 Presidential campaign,
with the specic aim to promote a sense of civic duty and national unity (Zaretsky, 2018). Macron’s
legislative proposal became law in 2018. In Germany, both mainstream and populist parties have set
o debates on reintroducing conscription to tackle the progressive deterioration of social cohesion
and national values. The former Commissioner for the Armed Forces - and SPD member - Eva Högl
spurred a heated debate by arming that “ending conscription was a big mistake”, in alignment with
members of the CDU, as well as with the majority of members of the main German populist party
(AFD).
3
Similarly, a UK government-commissioned report by military historian Sir Hew Strachan in
2020 concludes that returning to a compulsory national service would address a lack of “mature
public engagement”.
4
The belief that reinstating military conscription would inculcate positive
attitudes towards national institutions in millions of young citizens can be traced in many of those
1Available online: https://bit.ly/3EPyNII.
2Available online: https://bit.ly/3pUIE9A and https://bit.ly/31X1B38.
3
Available online:
https://bit.ly/3msNZBP
,
https://bit.ly/3fHksEt
,
https://bit.ly/
3ykgJUD and https://bit.ly/3GvDGXM.
4Available online: https://bit.ly/2HZckjY.
1
countries that discontinued military conscription.5
At rst sight, the enthusiasm of those politicians and experts leading the current debate on labour
military policies seems to be grounded. Taking place at a very sensitive time of one’s life, and
isolating young citizens from society for a substantial number of months, military conscription
does have the potential to shape attitudes towards the state. However, to date, there exists neither
theoretical consensus nor empirical validation to ascribe current patterns of decreased institutional
trust to the abolition of universal military conscription. This paper investigates whether ending
military service shaped individuals’ condence in the political institutions that conscripts are
instructed to serve.
Scholarly work provides only some support to the hypothesis that military conscription would
reduce the widening gap between the citizen and the state. Its advocates argue that conscription
would “reinstill the sense of shared national mission and community that is at present allegedly
absent” (Krebs, 2004, p.89), leading young individuals to develop an appreciation of the “civic
whole” (Moskos et al., 1988). By introducing conscripts to other segments of the population and
by transmitting them a state civic identity (see e.g., Levi, 1997), conscription is expected to cement
loyalties to the polity (Leander, 2004; George and Teigen, 2008; Juan, Haass, and Pierskalla, 2021).
If subscribing to this argument, we should expect ending military conscription to have decreased
institutional trust. Yet, a substantial number of scholars in the eld of civic-military relationships
are rather skeptical of the romantic idea that the military can serve as a “school for the nation”
(Krebs, 2004). Instead of aligning the citizen with state institutions, conscription may produce the
opposite eect, as soldiers “dene their identities and loyalties with reference to the military as a
distinct institution” (Kadercan, 2013, p.126), prioritizing parochial interests over broad, national ones
(Rosen, 1995; Rhodes, 1995). If this is the case, we should expect that ending military conscription
has increased, rather than decreased, institutional trust.
Against this background, this paper explores the eect of discontinuing military conscription
5
See e.g.,
https://bit.ly/3nOqqnG
,
https://bit.ly/2TN2AMd
, and
https://bit.ly/
361dFjM
. Note that this debate is not unique to Europe. For example, Gulf states are increasingly relying on
conscription to enhance national identities (Ardemagni, 2018).
2
on institutional trust in European countries. This is an open, non-trivial, policy-relevant question,
which has implications for the ongoing debate over whether reintroducing military conscription
might help ghting the decades-long erosion in trust towards representative institutions. We
address this question using a three-steps empirical design that seeks to safeguard at the same time
internal validity, threatened by unobserved heterogeneities in military recruitment, and external
validity, which would be limited if focusing on a specic conscription system. We rst assemble
a dataset on conscription policies across 15 European countries, and identify the “pivotal” cohort
for each of them, i.e., the rst cohort of citizens aected by the reform ending conscription, based
on their year of birth. While ending conscription is a political choice taken at the country level,
and so endogenous to an evolving political context, policy variations are as good as random at the
individual level. We then leverage individual-level data on attitudes towards institutions from the
European Social Survey (ESS). Using a Regression Discontinuity design, we compare the attitudes
of individuals born just before the pivotal cohort - the “conscripts”, our control group - against
those of individuals born just after the pivotal cohort - the “civilians”, our treatment group. Given
the presence of man-only conscription, we also look at the eect of the conscription reforms on
men vis-a-vis their eect on women within the same cohort, expecting to detect no impact on the
institutional trust of the latter. Finally, to account for country-specic unobservable characteristics
and for time-varying dynamics of institutional trust, we include country and ESS-wave xed eects.
A key result emerges: cohorts of men that reached the drafting age just before the abolition
of conscription exhibit lower trust than comparable cohorts of men that were just exempted,
whereas no eect is found among women within the same cohorts. In particular, ending military
conscription signicantly increases trust in the country’s legal system, parliament, political parties
and politicians by, respectively, 5.1%, 6.47%, 6.25% and 4.15%, relative to the unconditional mean.
Treatment eects are stronger in post-socialist countries, where the level of democratization was
lower and conscription was abolished more recently, compared to Western European states. Our
ndings, which are robust to a wide array of robustness checks, hence show that ending conscription
did aect institutional trust, but not in the direction lamented by those advocating its reintroduction.
3
We explore three potential mechanisms through which not being conscripted may increase
institutional trust later in life. Theoretical arguments that conceive conscription as an institution
with the potential to inuence recruits’ long-run attitudinal patterns emphasize the role of military
culture in creating a cohesive, homogeneous community with uniform values and attitudes, coa-
lescing young men around the primacy of the military over mistrusted democratic institutions (see
e.g., Krebs, 2004; Juan, Haass, and Pierskalla, 2021). Following these arguments, we should expect
attitudes towards institutions to be more homogeneous among conscripts, and more polarized
among non-conscripts. We nd robust evidence supporting this claim. Ending conscription may
also lower the opportunity cost of skill development, so higher trust among non-conscripts may also
reect endogenous changes in schooling choices (see e.g., Di Pietro, 2013). Our ndings, however,
suggests that this socio-economic mechanism is unlikely at play. Finally, we show that results
are not channelled by either context-specic evaluations of the executive in charge at the time of
the interview, nor by the political leaning of the government discontinuing conscription in the
rst place. In sum, ending conscription likely increased institutional trust via the transmission of
military culture, rather than by shaping educational choices or government popularity.
Our contribution bridges the literature on military conscription with that on the long-run
determinants of institutional trust. Existing empirical papers on conscription and civil-military
relations rely on specic drafting systems (e.g. the Argentinian lottery, the Vietnam draft) to
study the “civil-military” gap in partisan orientations, political participation and authoritarianism,
resulting in strikingly dierent conclusions (Erikson and Stoker, 2011; Horowitz, Simpson, and
Stam, 2011; Green, Davenport, and Hanson, 2019; Navajas et al., 2020). We focus instead on attitudes
towards those national institutions that the military is instructed to serve, and build our inference
on 15 dierent countries. While proponents of conscription in the absence of territorial threats
motivate it as a tool to foster civic sense, we show that its reintroduction would most likely yield
the opposite eect, contributing to the erosion of trust towards institutions. This nding adds to
the ever-expanding literature on the long-run determinants of trust (Anderson and Paskeviciute,
2006; Keele, 2007; Dinesen, Schaeer, and Sønderskov, 2020).
4
Conscription and trust
In the absence of territorial threats, the rationale behind military conscription is to incorporate
the ordinary citizen - specically, the ordinary young man - in the high-politics domain of state
coercion. Conscription represents a cornerstone in the political socialization of men: at a critical
stage of life, they are immersed in an extensive, long-lasting program, in which their “civilian status
is broken down and the new identity of military recruit is forged” (Jackson et al., 2012, p.271).
The military experience aects the recruits’ personality traits, beliefs, and behavior (Jackson et al.,
2012; Horowitz and Starn, 2014; Navajas et al., 2020), and can shape the attitudes and voting patterns
of politicians, particularly if they served in higher military ranks (Stadelmann, Portmann, and
Eichenberger, 2018). It can also generate a “civil-military gap”, i.e., a distance in the sociopolitical
beliefs and values held by military personnel relative to civilians (see Brooks, 2019, for an extensive
overview). In the short run, the “civil-military gap” can aect the public scrutiny over - and
accountability of - the armed forces (Fordham, 2001). In the long run, it can redene the relationship
between the military and the state more broadly (see e.g., Feaver and Gelpi, 2005).
How does military conscription - and its abolition - aect the “institutional civil-military gap”?
In this section, we develop two competing perspectives.
Promoting civic virtues
One strand of the literature in civil-military relationship holds that, by “bonding citizens [..] and
providing civic skills” (George and Teigen, 2008, p.342) and thus reinvigorating “the civic-mindedness
that they believe characterized earlier generations” (Krebs, 2004, p.89), conscription forms “loyal
and virtuous citizens” (Leander, 2004, p.576). Scholars in this tradition believe conscription to have
served a democratizing function, helping to integrate the military into newly-formed nation-states
(Dier, 2010), and welcome the bond of loyalty between armed forces and democratic institutions
enshrined in a number of modern constitutions.
5
The expectation that conscription promotes transferable civic virtues builds on an optimistic
assessment of two cornerstones of the military experience: the top-down transmission of national
values from the elite to the draftees, and the bottom-up convergence emerging from the interaction
among draftees of dierent socioeconomic background. The rst mechanism envisages conscription
as a “a great national school in which the ocer would be an educator in the grand style, a shaper
of the people’s mind” (Krebs, 2004, p.92). As a “total institution”, conscription isolates young
individuals with highly unstable political opinions from society at large, disciplining their behaviour
by enforcing military norms via both formal ordinance and informal praxes. Due to the increased
awareness of one’s bonds with the country, and to the ultimate sacrice military service may
demand of the conscript (Grossman, Manekin, and Miodownik, 2015), military training inculcates
in the youth values of loyalty, patriotism and a respect for the law (Huntington, 1981).
The second mechanism is expected to shape draftees’ attitudes via intergroup contact. Drawing
recruits from virtually all social groups, conscription instils a collective sense of duty from which no
one is exempted (Poutvaara and Wagener, 2011b; Choulis, Bakaki, and Böhmelt, 2019). Prominent
proponents of military conscription like Janowitz (1983) regard the military as generating intense
interactions between individuals from varied backgrounds during their “impressionable” years, often
to execute cooperative tasks. By forging closer ties across diverse sub-populations, and exposing
conscripts to the national community, military service demands that “members of a polity be loyal
to the community and to its values, rather than to the traditional values of family or clan” (Leander,
2004, p.576). Conscription forces individuals to reconsider their identity, their personal attachments
and their denition of the political community, and in doing so it develops a state civic identity and
loyalty towards the institutions.
Military training and the political socialization thereof are believed to boost civic obligations
towards the state and its institutions, and thus abolishing conscription could lead to a deterioration
in civic “mindedness”. In line with this argument, we seek to test the following hypothesis:
H1a: Ending military conscription decreased long-run institutional trust.
6
Opposing checks and balances
Whereas one of the most conventional and popular justications for the reintroduction of compulsory
military service is derived from its role in forming polities and producing virtuous citizens, many
contemporary scholars take issue with such “myth”, emphasizing the lack of consistent evidence
(see e.g., Krebs, 2004; Leander, 2004).
Particularly relevant for our study, while the military’s rst task is to protect the citizen, its
coercive power makes it a potential threat for democracy. This leads to a civil-military relations
paradox: “[...] a variant of the basic problem of governance that lies at the core of political science:
making the government strong enough to protect the citizens but not so strong as to become
tyrannical” (Feaver, 1999, p. 214). The introduction of a mandatory military service can be used as a
powerful instrument for mass indoctrination, with the specic aim of bolstering regime resilience
(Juan, Haass, and Pierskalla, 2021). And as Poutvaara and Wagener (2011b, p.165) point out, “not
only were conscript forces used by totalitarian regimes (Nazi-Germany, the Soviet Union, or Fascist
Italy) without noticeable resistance from within the army, but also democratic countries [...] used
conscription at the time of their military coups”. The threat of a tyrannical military has been
traditionally minimized by clustering soldiers away from competing societal organisations (Rosen,
1995). On the one hand, this reduces the risk of subversive alliances between the military and part
of society. On the other, isolating soldiers fosters their loyalty towards and identication with the
armed forces, at the expenses of their allegiance to those institutions they are instructed to protect
(Rosen, 1995).
As a matter of fact, whereas the extent to which military education inculcates civic virtues is
disputable, there is little doubt about it instilling traditional military virtues (Finer, 2002; Leander,
2004). The development of a sectarian military culture is not solely the unintended consequence
of geographic segregation during the conscription period, but is deliberately strengthened by the
military organisation itself, through both behavioral practises and rational arguments. The extensive
training and social rituals recruits must endure shape their civic identity along military norms
7
(Finer, 2002; Varin, 2014). In the words of Kier (1995, p.69), “[f]ew organizations devote as many
resources to the assimilation of their members. The emphasis on ceremony and tradition, and the
development of a common language and esprit de corps, testify to the strength of the military’s
organizational culture”. Obviously, young men join the military with heterogeneous ex ante beliefs.
In some cases, those beliefs could be strong enough, despite the young age, to “resist” the military
culture, but the emphasis on comradeship around military norms and social cohesion are likely
to lead to beliefs’ homogeneity. This powerful assimilation process coalesces soldiers around a
set of focal norms placing armed forces above political institutions (Kier, 1995). It does not come
as a surprise that, while the military represents a highly trusted institution in most democracies
(Choulis, Bakaki, and Böhmelt, 2019), its personnel often exhibits disparaging attitudes toward civil
society (Feaver and Kohn, 2001; Stadelmann, Portmann, and Eichenberger, 2018).
Conscripts are exposed not only to the identity of the military, but also to its organizational
interests (Kadercan, 2013). Among these there are the preservation of domestic political power, as
well as the acquisition of additional institutional autonomy and inuence over a range of issues, from
the organization of national security to the appointment of key institutional gures (Huntington,
1981; Bove, Rivera, and Rua, 2020). As political actors subordinate the military to their democratic
authority, the latter often claims institutional prerogatives that can lead to disputing such authority,
particularly within specic policy domains that bear on the military itself (Brooks, 2019). Being
the unique responsible of the “management of violence”, the military represents an exceptional
body within democratic societies, whose prerogatives clearly dierentiate it from other institutional
actors. In sum, the military experience may foster distrust around institutions of civilian oversight,
as they represent an undesirable constraint to its organisational scope of action. Altogether, these
arguments lead to the formulation of a second, competing hypothesis:
H1b: Ending military conscription increased long-run institutional trust.
8
Empirical analysis
Identification strategy
For our analysis, we leverage information on 15 reforms that discontinued compulsory military
service in Europe throughout the second half of the 20
th
and 21
st
century. We then use individual-
level data to compare institutional trust in cohorts of men just young enough to avoid the compulsory
military service to institutional trust in cohorts of men born not quite late enough to be aected by
the reform.6
Denote by
Tx,c
the treatment variable for individuals born in cohort
x
and country
c
, taking
value
1
if individual
i
was aected by the reform ending conscription, else
0
. Also, denote by
rx,c
the “running variable”, given by the absolute distance in years from the “pivotal” cohort. We then
use a Regression Discontinuity (RD) design to test:
yi,x,c,w=α+βTx,c+f¡rx,c¢+θc+µw+²i,x,c,w.(1)
where
yi,x,c,w
is the institutional trust of individual
i
born in cohort
x
and country
c
, interviewed
during the
wth
ESS wave. Our main coecient of interest,
β,
captures the local causal eect of
the treatment on institutional trust. In the main specication,
β
is estimated using a local linear
regression, a rst order local-polynomial to construct the bias-correction, a triangular kernel
function to construct the local-polynomial estimator, and the standard Mean Squared Error optimal
data-driven bandwidth selector (Calonico et al., 2017). As trust may exhibit idiosyncratic patterns
over space and time, we apply both country (
θc
) and ESS wave (
µw
) xed eects. Since in each of
the sampled countries only men were conscripted, we test our main hypotheses through equation 1
among self-reported men, and compare our ndings with those obtained using the subsample of
self-reported women.
6
Such approach has been widely used in the domain of compulsory schooling reforms (e.g., Marshall, 2016; Cavaille
and Marshall, 2019).
9
We expect any discontinuity around the end of conscription to be more discernible among men.
Note that while this comparison strengthens the reliability of our inference, we cannot assume that
women’s time-varying institutional trust could be taken as a missing outcome, and thus that, in
the absence of conscription, men in the treatment group would have followed the same trend in
institutional attitudes as women. Several studies show that, alike ideological attitudes (Erzeel and
Celis, 2016), trust towards society in general and institutions in particular (see e.g., Ulbig, 2007) are
aected by gender, for example through the gender-gap in political representation. To account for
this, our RD strategy allows time-bandwidths to be chosen separately for the two sub-groups. As
such, we do not make any assumption about the potentially gendered time-trends in institutional
trust (see Dinas and Stoker, 2014, for an extended discussion).
Dependent variable: Institutional trust at the individual level data
Information about individual-level trust towards the country’s institutions is taken from the nine
rounds of the ESS, running every two years between 2002 and 2018 and covering 33 European
countries. We use the following question:
Do you trust the legal system (parliament/parties/politicians)?
0: Not at all ; ... ; 10: Completely.
The chosen items are arguably the most frequently used markers of institutional trust (i.a., Citrin
and Stoker, 2018). Our main dependent variable, labelled “institutional trust”, is based on the
principal-component-analysis (hereafter
PC A
) of the survey items presented above (see e.g., West,
2017, for a similar approach). Institutional trust is the rst component of the PCA (normalized
between 0 and 1 to facilitate the interpretation of results), and increases in each single item. Since
answers to the four questions are highly correlated with each other,
7
the rst component of the
7
Not surprisingly, the correlation between trust in parties and politicians is the highest one (87.1%). Trust in
parliament is also highly correlated with both trust in parties (70.0%) and politicians (72.4%). Trust in the legal system is
less collinear with the other proxies, but even in this case correlations remain quite high: 62.5% with trust in parliament,
56.4% with trust in parties, 58.1% with trust in politicians.
10
PCA yields similar, positive weights for each trust item, and captures a high fraction of the overall
variance.
8
Our proposed metric thus suitably captures institutional trust, while allowing us to keep
the presentation of ndings concise. We provide results separately for each single trust item in the
Supplementary Information (SI), section C.4 (p.11).
We remove ve sub-groups of respondents from the pool of ESS observations, as their inclusion
might be problematic for our estimation strategy. Specically, we drop: (i) individuals who have
opted for a professional military career, due to self-selection issues; (ii) individuals that might
not have been conscripted due to their citizenship status; (iii) individuals born in Sweden after
1999, hence aected by the 2017 re-activation of conscription; (iv) individuals from Croatia and
Luxembourg, due to limited data;
9
(v) individuals with a university degree, due to the possibility to
postpone conscription in the majority of our case studies.
10
This leaves us with 161,623 respondents
from 15 European countries, which have abolished conscription between 1961 and 2012. Importantly,
none of these sampling choices would change our results. In the codebook which is part of the
replication material, we provide a detailed description of our subsampling strategies, present the
summary statistics for our data, and discuss our choices on conscription reforms when confronted
with discrepancies between the dierent sources employed.
Independent variable: Conscription reforms at the country level
The popularity of universal, compulsory military service experienced historical highs and lows.
While active in Mesopotamia as far back as 1750 B.C., the modern revival of the draft in Europe
originated in the aftermath of the French Revolution. At the time of writing, about 60 countries
worldwide keep a program drafting people in their military (Desilver, 2019). After being widely
8
Specically, the weights are 0.5022, 0.5183, 0.5267, and 0.4491 for resp., trust in parliament, parties, politicians, and
the legal system, capturing 76,43% of the overall variation.
9These countries have only been sampled twice by the ESS.
10
Pursuing tertiary education allowed conscripts to delay the start of military service in many countries, hence
shifting the formal eligibility criterion away (Stolwijk, 2005). Therefore, those with tertiary education who reached the
eligible age before the approval of the legislation that ended conscription may be incorrectly included in the control
group. In our main estimation, we exclude individuals with a university degree from the analysis. While their inclusion
lowers the magnitude of our main estimates (see SI C.2, p.9), this sampling choice helps closing the gap between
eligibility and treatment status, thereby minimizing attribution issues, at the expense of representativeness.
11
used throughout the 20th century, the European countries we analyse discontinued conscription
from 1995 onwards, with the notable exception of the United Kingdom, where it was abolished in
1961 (see timeline in Figure 1).
Although the European countries that decided to replace conscription with an All-Volunteer
Force (AVF) undoubtedly did so following a domestic debate, defense scholars point towards a
common, overarching incentive: the need to replace obsolescent mass-armies in the wake of the
geopolitical change brought upon by the end of the Cold War, which dramatically reduced the risk
of large-scale interstate conicts in Europe.11
Volunteer militaries were also better suited for the new generation of high-technology, expe-
ditionary and multi-national NATO and UN missions characterizing the post-Cold War world,
compared to poorly-equipped mass armies (Haltiner and Tresch, 2008; Poutvaara and Wagener,
2011a). Divorcing warfare activities from border defense dramatically weakened the policy rationale
behind military conscription. In the words of Haltiner and Tresch (2008, p.172): ”citizen-soldiers
were formally and traditionally considered ideal defenders of their national territory; they are,
however, not considered suited to the new kind of multinational military missions abroad. No
European people would be ready to legitimize the compulsory employment of young conscripts in
missions out of national or alliance territory..12
11
Military conscription is often a response to deteriorating international security. Most of the countries that did
not discontinue conscription, such as Finland, Greece or Norway, are still involved in territorial disputes. And amid
rising regional tensions, Sweden and Lithuania decided to reintroduce a military draft. Available online:
https:
//bit.ly/339XKxH and https://bbc.in/3IwhiiD.
12
In addition to strategic considerations, economists converge in describing military conscription as “inecient”
compared to voluntary service, which exhibits relatively longer tenures, minimizing turnover costs, and does not
involve any coercive recruiting mechanism. Conscription also disregards individuals’ relative skills, violating established
principles of labor market productivity via specialization (Hall and Tarabar, 2015). Similar negative views about military
conscription arise when considering issues of intergenerational equity (Poutvaara and Wagener, 2007; Poutvaara and
Wagener, 2011b).
12
Figure 1: Timing of reforms across Europe.
End of WW2 United Kingdom
End of
Cold war
1945 1961 1991
Belgium
Netherlands
Germany
France
Spain
Sweden Bulgaria
Slovenia Poland
Czech Republic
Hungary
Italy
Portugal
Slovakia
1995 1997 201220022001 20082006 20092005
Note: Based on an update of Toronto’s (2007) military recruitment dataset. The codebook which is part of the replication
material provides extensive summary statistics and some contextual description for each reform.
In line with their tradition of pioneering liberal change, Belgium (in 1995) and the Netherlands
(1997) were among the rst countries to abolish conscription, leading to a rst wave of reforms -
lasting until 2005 - that involved all of the sampled Western European countries but Germany. A
second wave, taking place between 2004 and 2009, saw Central and Eastern European countries
moving from conscription to AVFs (Bove and Cavatorta, 2012). The relative delay with respect to
Western countries has to do with the broader transformation former USSR allies experienced with
the collapse of the Soviet Union, which led to an agenda of increasing integration between Western
and Eastern Europe. Ten former members of the so-called “Warsaw Pact”, in fact, chose, upon their
independence, to move from the Soviet to the Western security umbrella, joining NATO.
13
By 2005,
six of them had already adopted AVFs. Abolishing conscription was such an important reform for
countries like Hungary and Czechia, that they anticipated the transformation to an AVF from the
deadline that had been set initially (George and Teigen, 2008).
For our RD strategy, the two key pieces of information that jointly identify the “pivotal cohort”
13
Whereas Western countries - except Sweden - had been already NATO members for decades when conscription was
halted, every Central and Eastern European country in our sample joined NATO just a few years before discontinuing
military conscription.
13
- the rst one to be exempted from conscription - are: (a) the date in which the reform ending
conscription was implemented in each country, and; (b) the age at which young men were required
to serve. The former information is retrieved from the “Military recruitment dataset” (Toronto, 2007;
see also Asal, Conrad, and Toronto, 2017 for a recent application), which we extend to include seven
countries where conscription was suspended after 2007, using data from War Resisters’ International,
a global network of grassroots pacist groups.
14
The latter is based upon the C.I.A. World Factbook
(CIA, 2020), an archive providing the required ages for voluntary or mandatory military service and
the length of service obligation for each of the countries in our sample.
Results
Figure 2displays the eect of ending conscription on institutional trust. Institutional trust is proxied
by a single composite index obtained through the rst component of a PCA that combines trust in
legal system, parliament, parties, and politicians. We begin by looking at the sub-sample of men
in Figure 2a, where we estimate
ˆ
β=0.026
, signicant at 1%. Ending conscription did not lead to
distrust towards the state, as those proposing its reintroduction would implicitly suggest. Quite on
the contrary, we detect a mild but nonetheless meaningful increase in institutional trust, later in
life, by about seven percentage points on the respondents’ scale.
As expected, Figure 2b shows that the end of conscription did not entail any eect on women
from the same cohorts. Comparing the z-scores of RD coecients with a standard t-test reveals that
the eect of ending conscription on men’s trust is signicantly higher than the eect on women’s
for each of the four trust items.
15
As shown in SI C.4 (p.11), the main nding holds across each of
the individual trust items.16
14
We retrieved novel information for the following countries (rst year without conscription in parentheses):
Bulgaria (2008), Poland (2009), Sweden (2011). Conscription in Sweden was then re-activated in 2017. See
https:
//wri-irg.org/en/ for detailed country reports.
15
Specically, the z-scores are: 2.03 for the legal system, 1.90 for parliament, 2.27 for parties, and 1.32 for politicians.
16
We do not detect any informative heterogeneity when we analyze each of the 15 countries in our sample individually.
We nd strong evidence in support for H1b in Czechia, Germany, Italy, Portugal and the UK. In the remaining countries
the eect has the expected sign but is largely insignicant, given the rather limited statistical power due to a lower
number of observations within each country.
14
Figure 2: End of conscription and Institutional trust.
(a) Men (b) Women
Note: Figures are obtained using the rdrobust package developed by Calonico et al. (2017), based on IMSE-optimal binning and triangular dummy
weights. 95% condence interval. In Subgure 2a on the left, we estimate ˆ
β=0.026, signicant at 1%, with SE =0.008 and a bandwidth including
male respondents who reached the minimum age for serving in the army in the 7 years around the date in which conscription was abolished (n.
12,523). In Subgure 2b on the right, the eect of ending conscription on institutional trust ( ˆ
β=0.008,SE =0.007), with a bandwidth of 9 years
and a sample of 14,792 women. Country and ESS-wave xed eects apply.
While all our sampled countries discontinued conscription under a democratic regime, six out of
fteen countries (Bulgaria, Czechia, Hungary, Poland, Slovakia, and Slovenia) were members of
the Warsaw Pact until the collapse of the Soviet Union. The political and historical context within
which reforms ending conscription took place across the post-socialist block in our sample dier in
two important ways.
Firstly, despite the enactment of important reforms, in the years of the transition to AVFs (between
2004 and 2009), former members of the “Warsaw Pact” lagged behind Western democracies with
respect to several democracy indexes, and particularly to the pervasiveness of military and political
corruption. For example, the V-Dem corruption index was on average more than four times higher
in the six post-socialist countries in our sample, compared to the nine Western ones
17
, while, the
“Global Corruption Barometer” computed by Transparency International
18
reports that perception
of corruption of the military to be 17% higher in ex-Warsaw pact republics. In a similar vein, all
17Available online: https://www.v-dem.net/en/.
18
Available online:
https://www.transparency.org/en/gcb
. Authors’ calculations are provided in
the replication material.
15
post-socialist countries are labelled as “awed democracies”, e.g., by the index developed by the
Economist Intelligence Unit.19
Secondly, labor military policies in post-socialist countries dier signicantly from those in
Western ones: in the former, in fact, the abolition of military conscription was part of a broader
reorganization of defence policies, and occurred later in time. After the end of the Cold War,
post-socialist countries had to profoundly revisit institutional checks and balances as part of their
democratization process, which involved also the military (Dunay, 2005; Latawski, 2005; Kříž,
2007; Malešič and Vegič, 2009; Čižik, 2021). In many post-socialist democracies, citizens saw the
conscription system as an emblematic relic of the corrupted, pre-democratic era.20
To the extent to which their shared post-socialist (or communist) history intensies the eect of
discontinuing conscription, we should recover dierences in the intensity of the treatment eect
between the six ex-Warsaw Pact and the nine Western European countries in our sample. We
evaluate the eect of ending conscription on trust across the two blocks in Figure 3. Our ndings
are rather reassuring: while the treatment eect is indeed higher among post-socialist countries, it
remains positive and signicant among men - while non-signicant among women - in both blocks.
19Available online: https://www.eiu.com/n/.
20
In Russia, were conscription remains active to this date, it has been reported that, whereas men from the rural
reaches of the country are unlikely to avoid conscription, auent families often press ocials to exempt their children.
Available online: https://econ.st/2ZRpVTD.
16
Figure 3: Post-socialist vs. Western countries.
(a) Men, Post-socialist (b) Women, Post-socialist
(c) Men, Western (d) Women, Western
Note: Figures are obtained using the rdrobust package developed by Calonico et al. (2017), based on IMSE-optimal binning and triangular dummy
weights. 95% condence interval. In subgure 3a on the top-left we estimate ˆ
β=0.030 (signicant at 5%), SE =0.014, bandwidths of 6 years,
n. 4,713 men. In subgure 3b on the top-right we estimate ˆ
β=0.010 (non-signicant), SE =0.011, bandwidths of 8 years, n. 5,526 women. In
subgure 3c on the bottom-left we estimate ˆ
β=0.019 (signicant at 5%), SE =0.009, bandwidths of 9 years, n. 9,019 men. In subgure 3d on the
bottom-right we estimate ˆ
β=0.006 (non-signicant), SE =0.008, bandwidths of 9 years, n. 8,740 women. Country and ESS-wave xed eects
apply.
Threats to identification
In the Supplementary Information (SI), we begin by assessing the validity of our RD design (SI A,
pp 2-4). Performing standard density and continuity tests conrms the absence of sorting around
the discontinuity (A.1 and A.2, pp 2-3). We also look into the possibility that educational, scal and
labor market policies implemented in the same year as the conscription reforms, and potentially
exerting a long-run gendered impact on institutional trust, may act as cofounders (A.3, p.4), nding
17
no support for this hypothesis. Second, we test the robustness of our analysis to dierent modelling
choices (SI B, pp 6-7), demonstrating that the reported ndings are robust to the use of, respectively,
alternative bandwidths, polynomial orders and RD weights (B.1 and B.2, pp 6-7). Results are robust
to alternative country sampling (i.e., dropping one country at a time, C.1, p.8), to alternative unit
sampling (i.e., including respondents who completed tertiary education, C.2, p.9), and to placebo
reform dates (C.3, p.10). As mentioned above, we also show that results hold up well to considering
each of the four trust items composing our index separately (C.4, p.11). Altogether, these tests
give us condence that our estimates are unlikely to be spuriously driven by sorting around the
treatment, underlying time-trends, outlier countries or specic trust items.21
Finally, SI D (pp 12-19) explores the heterogeneity of the treatment both in terms of policy
graduality (D.1, p.12), reform date (D.2, p.17), socio-economic backgrounds (D.3, p.18), and political
views of the government approving the reform (D.4, p.19), recovering larger coecients for reforms
enacted sharply and more recently, for individuals with higher socioeconomic background. It is
worth pausing on this last battery of robustness checks. Since the treatment status is based on
formal eligibility, rather than participation status, our estimates must be understood as an intention
to treat. We explain here how policy graduality may drive the discrepancy between de jure and
de facto treatment status. Overall, these threats to identication make false negatives more likely
relative to a fully randomized experiment.
We account for the possibility that the actual implementation of the policy - which is the threshold
upon which individuals are assigned (or not) to the treatment group in our analysis - might
have occurred later than the approval of the legislation discontinuing conscription. Especially in
countries opting for a gradual phaseout period, governments’ eort to mobilize conscripts might
have weakened following the approval date (Stolwijk, 2005), decreasing the number of conscripted
21
Findings are also robust to controlling for the duration of enlistment each respondent faced. Country xed eects
cannot in fact account for the possibility that the length of conscription may have varied over time. We retrieve yearly
information on terms of service for each country from Toronto (2007), merge it with our survey using (CIA, 2020)
data on conscription ages, and nd that our estimates remain largely unchanged when controlling for months of
enlistment. Because of space limitations, these tables are not included, but can be reproduced using the replication
material provided.
18
individuals and, therefore, possibly biasing our estimated eect towards zero. To assess the extent
of the measurement error arising from our eligibility-based intention to treat, we collect qualitative
information about the date of approval of each reform, as well as quantitative administrative and
survey data about the number of conscripts in each of the sampled countries, in the years before
the formal end of conscription. Results displayed in SI D.1 (p.12) show how countries in which
the distance between approval and completion of the conscription reform was one year or less
display a 14.3% higher treatment eect, compared to those adopting a longer phaseout period. The
smaller eect we retrieve in countries where implementation took longer might be due laxer policy
enforcement in the phaseout years, which made draft avoidance relatively easier. As a result, our
coecient - i.e., an intention to treat - is more likely to mis-classify as conscripted (i.e., members
of the control group), individuals who avoided the military service (i.e., the treatment group). If
anything, this exerts a downward bias on our aggregate estimated treatment eect.22
How conscription affects institutional trust
Military culture
We have shown that ending conscription increased institutional trust. Common to the theoretical
arguments presented in the second section of the paper is the belief that conscription drives
recruits’ long-run attitudinal patterns by transmitting a set of core military values. The resulting,
gradual adjustment of draftees to the dominant military culture should ultimately produce a rather
22
An additional reason why some individuals in conscripted cohorts - our control group - may not have received
military training is due to the fact that, in most democracies, conscripted individuals are given the possibility to exert
conscientious objection to the military, and apply for alternative services. We argue that the edge between intention to
treat and treatment status is however small. Except for Slovenia, in all sampled countries the compulsory period of
alternative services was always longer than that of military conscription, in order to discourage draftees from resorting
to conscientious objection. For a similar reason, governments typically granted a lower compensation to objectors,
relative to their military counterparts (for an extensive review, see Smith, 2004). As a consequence, the share of young
men choosing to apply for alternative service has generally been very small, and steadily below 5% in Belgium, France,
Portugal and the UK (Smith, 2004). Similar gures most likely apply to Bulgaria, Hungary, Poland and Slovakia, even
though, in these cases, available estimates come from experts’ reports (Stolwijk, 2005). Figures are slightly higher in the
Netherlands, were less than 8% among conscripted men applied for civilian service between 1982 and 1991, with 80% of
these being accepted. Similarly, in Sweden, the share of draftees applying for conscientious objection reached 10% in
the nal years in which conscription was in place. Finally, Germany, Italy and Spain represent the outliers among the
countries under scrutiny, exhibiting substantially higher shares of objectors among their conscripts (Stolwijk, 2005).
19
homogeneous community with uniform values and attitudes (see e.g., Krebs, 2004; Juan, Haass, and
Pierskalla, 2021). This military culture mechanism yields an important testable prediction: attitudes
towards institutions should be more homogeneous among conscripts, and more polarized among
non-conscripts.
We analyze the causal eect of ending conscription on the standard deviation of the distribution
of institutional trust among men and women. We begin by computing the country-wave average
institutional trust. Then, we take the squared dierence between each individual’s score and the
corresponding country-wave average (both normalized between 0 and 1). Finally, we test the eect
of our treatment - ending conscription - on such index, using the same estimation strategy of the
main analysis. Positive treatment eects would thus indicate that ending conscription increases the
diversity of opinions, and vice versa.
We nd evidence in support of this “uniformity mechanism”. Figure 4shows that ending conscrip-
tion exerted a positive and signicant impact on the polarization of institutional trust among men
(4a), with no comparable eect among women (4b). The increased polarization in men’s institutional
trust supports the idea that military conscription prompted more uniformed, negative views of civil
society among draftees, at a very sensitive stage of their life. Further analysis show that such eect
is driven, as one would expect, by those countries in which the policies ending conscription were
implemented more abruptly (see SI D.1, p.12).
20
Figure 4: Polarization of institutional trust.
(a) Men (b) Women
Note: Figures are obtained using the rdrobust package developed by Calonico et al. (2017), based on IMSE-optimal binning and triangular dummy
weights. 95% condence interval. In subgure 4a on the left we estimate ˆ
β=0.007 (signicant at 10%), SE =0.004, bandwidth of 10 years, n.
16,899 men. In subgure 4b on the right we estimate ˆ
β=0.001,SE =0.003, bandwidth of 19 years, n. 28,235 women. Country and ESS-wave
xed eects apply.
Educational choices
Conscription and the end thereof may aect trust formation indirectly by altering educational
choices. The abolition of conscription might in fact exert an ambivalent eect on college enrollment
rates: positive, on the one side, as it possibly entails an opportunity cost for skill development (e.g.,
Cipollone and Rosolia, 2007); negative, as it could reduce the incentive to enroll as a way to postpone
(or avoid) the military (e.g., Card and Lemieux, 2001). The net eect of these countervailing forces is
often small, and sometimes indistinguishable from zero (Imbens and Klaauw, 1995; Di Pietro, 2013).
Yet, if the rst eect dominates, discontinuing conscription would increase educational attainments,
hence likely improve individual socioeconomic conditions and, in turn, institutional trust (see e.g.,
Gelepithis and Giani, 2020), thereby partly channelling our ndings.
We do not nd evidence in support of the opportunity cost mechanism just presented, which is
consistent with some empirical evidence (Di Pietro, 2013). The abolition of conscription entails a
non-signicant eect on either men’s or women’s number of years of completed education (see
Figures 5a and 5b).
23
Such nding replicates when considering dierent proxies for long-run skill
23
For this analysis, we re-include in the sample individuals with tertiary education, but discard respondents who
21
development, including occupational skill specicity, perceived household income and a dierent
operationalization of the education variable (i.e., an indicator taking value 1 if the respondent
completed tertiary education or above), all measured at the time of the survey.
24
While our dataset
is not equipped to estimate the eect of ending conscription on subsequent career decisions, this
analysis suggests that the opportunity-cost channel is unlikely to be the main mechanism through
which military service aects institutional trust.
Figure 5: Educational choices.
(a) Men (b) Women
Note: Figures are obtained using the rdrobust package developed by Calonico et al. (2017), based on IMSE-optimal binning and triangular dummy
weights. 95% condence interval. In subgure 5a we estimate ˆ
β=0.015,SE =0.115, bandwidth of 7 years, n. 15,292 men. In subgure 5b we
estimate ˆ
β= −0.118,SE =0.104, bandwidth of 7 years, n. 16,192 women. The estimated eects are statistically insignicant for both men and
women. Country and ESS-wave xed eects apply.
Government popularity
Our design builds on the idea that the lower institutional trust observed among former service-
men captures a stable , “diuse” mistrust, rather than a time-varying, “specic” evaluation of the
government in charge at the time of the interview (Hetherington, 1998; Keele, 2007; Zmerli and
Newton, 2008; Citrin and Stoker, 2018). The fact that point estimates and standard errors are very
similar across dierent trust items is reassuring: it suggests that our metric is unlikely to capture
contextual dissatisfaction for specic institutional branches at the time of the interview. Yet the
are studying at the time of the interview. While this sub-group cannot be exactly identied in the ESS, we exclude
individuals younger than 24 for whom no ISCO occupational code is reported in the ESS dataset.
24We provide the coding for these additional analyses in the replication material.
22
documented dierence in institutional trust between conscripts and non-conscripts may also partly
reect dierences in support for the executive.
We investigate whether military conscription aects specic support, captured by the contextual
evaluation of government performance on three key issues: economy, education and health.
25
To
ease the presentation, our dependent variable is again the (normalized) rst component of a PCA
between the three survey items. Figure 6shows that ending conscription had indeed no eect on
either men’s (6a) or women’s (6b) assessment of the performance of the government in charge at
the time of the interview. These additional analyses help ruling out the possibility that our ndings
are spuriously driven by attitudes towards the government in charge at the time of the interview, or
by potential, concurrent events, such as political scandals.
Our eect may also be capturing long-lasting patterns of support for the the government that
adopted the reform. Conscription might have been perceived as an unfair gender-specic burden
when it was abolished. As such, the last cohorts of conscripts could still display resentful evaluations
towards the political leaning of the government in charge at the time, whereas the rst cohorts of
exempted young men could still be grateful to that same government. If this was the case, then
the magnitude of our estimates should be larger when the executive in charge at the time of the
interview shares the same political leanings of the government adopting the reform. Respondents
may in fact be more likely to incorporate, in these cases, specic mistrust towards the executive in
their responses, aecting in turn their diuse levels of trust towards the institutional system.
We explore this possibility by leveraging the interview date of each respondent, as well as
information from ParlGov (Döring and Manow, 2021) about the ideological orientation of the
government in charge, both at the time of the reform adoption and at the time of each interview.
We do not nd support for this mechanism, as treatment eects are unaected by whether the
government in charge when the interview takes place shares (or not) the political leaning of the
government adopting the reform (SI D.4, p.19 and Codebook B.2, p.7).26
25
Respondents were asked the following question: “How do you rate the state of the economy/education/healthcare in
your country nowadays?”.
26
In SI D.4, p.19, we also show how results are robust when dierentiating between reforms adopted by, respectively,
23
Figure 6: Specific government performance.
(a) Men (b) Women
Note: Figures are obtained using the rdrobust package developed by Calonico et al. (2017), based on IMSE-optimal binning and triangular dummy
weights. 95% condence interval. In subgure 6a on the left we estimate ˆ
β= −0.000,SE =0.006, bandwidth of 9 years, n. 16,577 men. In subgure
6b on the right, ˆ
β=0.001 ,SE =0.005, bandwidth of 10 years, n. 17,799 women. The estimated eects are statistically insignicant for both men
and women. Country and ESS-wave xed eects apply.
Conclusion
The debate around the possibility of reintroducing a compulsory military service has been particu-
larly lively in recent years. Politicians advocating in its favour have long argued that reintroducing
conscription is an eective mean to bring the citizen closer to the nation. In this article, we con-
tribute to such discussion by asking whether ending military conscription has aected institutional
trust in European countries. The answer to this question is not clear-cut ex ante, as conscription
exposes individuals to socialization processes with seemingly complementary objectives. On the
one side, it is intended as an experience boosting values of service and civic obligations towards the
state; on the other, the same socialization processes, taking place in highly structured organizations,
distant from society, shape civic identity along military norms. This creates a strong identication
with the armed forces, possibly clashing with loyalty towards democratic institutions.
Building on a quasi-experimental design, we demonstrate that reintroducing military conscription
right-wing and left-wing executives. In the replication material, we show how estimates remain the same when
removing from the sample the interviews occurring in the years around the reform adoption (N=13,030). Unfortunately,
only 370 men aged 17-19, from nine countries, were interviewed in the 365 days around the reform adoption date,
making any inference on this subset of respondents problematic.
24
as a way to foster civic sense would likely yield the opposite eect. We nd that cohorts just exempted
from conscription did not develop more negative attitudes towards the state, but actually exhibit
higher levels of institutional trust than cohorts who served compulsory time as soldiers, several
years after doing so. We demonstrate that the documented decrease in institutional trust is neither
the by-product of contextual government evaluations, nor the result of a change in educational
choices driven by the abolition of conscription. Instead, we show that the creation of homogeneous
communities with uniform views is likely at the root of lower diuse trust later in life.
Our article pieces together two strands of the literature, analyzing, respectively, the dynamics of
the “civil-military gap” and the long-run determinants of institutional trust. We contribute both
substantively and methodologically to the debate on the existence of a “civil-military gap” between
those who served in the military and those who did not. Substantively, whereas previous research
focused on personality traits (Jackson et al., 2012), ideological orientations (Erikson and Stoker,
2011; Green, Davenport, and Hanson, 2019; Navajas et al., 2020), or attitudes towards the use of
violence (Horowitz, Simpson, and Stam, 2011; Navajas et al., 2020), we focus on institutional trust.
The documented attitudinal divide we uncover is of key relevance, as it can undermine the stability
of the relationship between military institutions and society at large (see e.g., Brooks, 2019).
This paper also contributes to the literature that seeks to understand the determinants of trust.
Margaret Levi qualies trust as “a holding word for a variety of phenomena that enable individuals
to take risks in dealing with others, that solve collective action problems, or that promote willingness
to act in ways that seem contrary to standard denitions of self-interest” (Levi, 1996, p.1). In the
realm of politics, trust confers legitimacy to institutions, fostering compliance with the rule of law
among citizens. It is thus crucial “for the eectiveness and durability of democratic governments,
regimes that many today view as increasingly fragile” (Rathbun, 2011, p.50). It is hence by no
surprise that diminishing institutional trust is conceived as a major issue in liberal democracies
(Citrin and Stoker, 2018), prompting scholars to investigate its long-run determinants. We add to
this literature by focusing on the domain of high politics. That military conscription decreases
institutional trust highlights a policy paradox, warning against the somewhat popular idea that
25
reintroducing military conscription may solidify the relationship between the citizen and the state.
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Military Culture and Institutional Trust:
Evidence from Conscription Reforms in Europe
Supporting Information (SI)
Contents
A Validity of RD specication 2
A.1 Density test .......................................... 2
A.2 Continuity test ........................................ 3
A.3 Independence from simultaneous reforms ........................ 4
B Robustness to modelling choices 6
B.1 Alternative bandwidths ................................... 6
B.2 Alternative polynomial orders and kernel function ................... 7
C Robustness to sampling choices 8
C.1 Alternative country sampling ............................... 8
C.2 Alternative unit sampling .................................. 9
C.3 Alternative reform dates ................................... 10
C.4 Alternative trust measures ................................. 11
D Analysis of Heterogeneity 12
D.1 Heterogeneity by graduality of conscription phaseout ................. 12
D.2 Heterogeneity by reform date ............................... 17
D.3 Heterogeneity by socioeconomic background ...................... 18
D.4 Heterogeneity by government ideology ......................... 19
A Validity of RD specification
A.1 Density test
One concern with the RD design is that of potential selection around the threshold. As selection
into the pool of drafted is exclusively driven by the respondent’s birth year, we believe such concern
is not particularly relevant in our setting. Although our sample contains more respondents that
were eligible to be drafted than ineligible ones, Figure A1 shows that this is entirely driven by the
distribution of reforms over time, rather than potential strategic sorting. Consistently, running a
McCrary test (Calonico, Cattaneo, and Titiunik, 2014) on the pooled sample does not reject the
null hypothesis that the density of cohorts does not change at the reform (p=0.0078).
Figure A1: Density of the Data Either Side of the Conscription Abolition Year.
2
A.2 Continuity test
In this section, we look at the individual characteristics of respondents located at each side of
the reform date and, in particular, at their self-reported gender, parental education level, and
likelihood to take part to each of the 9 waves of the ESS. Results shown in Table A1 are obtained
via the estimation strategy used in the main paper and show how respondents on either side of
the discontinuity are on average statistically similar at the time of answering the survey. In other
words, the treatment has no eect on our pre-treatment covariates, thus supporting the validity of
our approach.
Table A1: Placebo Effect of End Conscription on Pretreatment Variables.
Gender Edu. Mother Round 1 Round 2 Round 3 Round 4 Round 5 Round 6 Round 7 Round 8 Round 9
Reform 0.001 0.030 0.001 0.006 -0.016** -0.016 0.000 0.005 0.010 0.004 0.002
(0.009) (0.024) (0.007) (0.008) (0.007) (0.010) (0.009) (0.009) (0.006) (0.007) (0.007)
N. 51345 31815 28158 28158 34959 24656 31581 28158 38324 34959 28158
Mean 0.50 2.56 0.08 0.11 0.11 0.13 0.13 0.13 0.10 0.11 0.09
Bandwidth 14 10 7 7 9 6 8 7 10 9 7
Polynomial 1 1 1 1 1 1 1 1 1 1 1
Country FE X X XXXXXXXXX
Notes.
p<0.10,∗ ∗ p<0.05, p<0.01
. Coecients are estimated using a local linear regression, dierent polynomial orders to construct the bias-correction, a
triangular kernel function to construct the local-polynomial estimator, and the standard Mean Squared Error optimal data-driven bandwidth selector (see Calonico
et al., 2017). Data for the main dependent and independent variables come from 9rounds of the European Social Survey (europeansocialsurvey.org).
3
A.3 Independence from simultaneous reforms
One may worry that the gendered, long-run responses of public opinion to the end of conscription
may possibly reect the role of confounding policies, that were implemented at the same time as
the legislation abolishing conscription and exerted a long-run, gendered impact on the institutional
trust of the same cohorts. While this is unlikely to be the case for all of the 15 countries in our
sample, this concern might still be relevant for a subset of them. In order to address this possibility,
we build on several extant sources to create a dataset of educational, scal and labor market
reforms that may indeed jeopardize our ndings. We then conduct a systematic search within the
data, matching, on a country-by-country basis, the date of approval of each of these reforms, with
the year in which conscription was abolished.
First, we consider educational policies, including both reforms of compulsory/secondary (see
e.g., Garrouste, 2010) and tertiary schooling (i.e., the “European Higher Education Area and
Bologna Process”), that may have aected the gender gap in enrolment. While none of the
sampled countries promulgated simultaneous compulsory-schooling and conscription reforms,
two countries (Hungary and Portugal) did implement the “Bologna” process (de facto shortening
the duration of bachelor degrees in an attempt to foster enrollment) at the same time as the
abolition of military conscription. Second, building on the Taxes in Europe Database (TED) of
the European Commission, we screened all the tax reforms with a potentially gendered impact in
each of the relevant country-year dyads. In this case, we were unable to nd any policy change
that could have induced eects similar as those discussed in our main analysis. Finally, we looked
at active labor market policies using LABREF, a descriptive database that records labour market
and welfare policy measures introduced by EU Member States since 1990.
1
In this case, we found
two possible matches. First, the Bulgarian Parliament approved a reform of both maternity and
paternity leave policies in December 2008. Following the reform, “maternity leave has increased
from 315 to 410 calendar days. Furthermore, working fathers are entitled to 15 days of paid
paternity leave to take care of a newborn child; this leave provision aims to encourage parents
to share their caring responsibilities. Fathers are also provided with an opportunity to share the
maternity leave with the mother, with the option of taking the remainder of the 410 days when
the child reaches six months of age." (LABREF). While this policy rarely concerns individuals
aged around 18 years-old - which are the focus of our analysis - some of our sampled Bulgarian
respondents may have beneted from the more generous leave provisions, that could have long-
run eects on mothers’ careers (see e.g., Troeger et al., 2020), future fertility decisions (Farré and
González, 2019) and, consequently, on the gender balance within the household (see e.g., Kleven,
Landais, and Søgaard, 2019; Kleven et al., 2019). Second, in 2002, Spain introduced a deduction for
1
For more information, see:
https://ec.europa.eu/social/main.jsp?catId=1143&
intPageId=3193.
4
women with children below the age of three engaging in salaried or self-employed work, for a
maximum annual amount of
1,200 per child (Law 46/2002). As for leave policies, the increase in
monetary benets for new mothers might exert a substantive, gendered impact on public opinion,
acting as a confounding factor for our estimated treatment eect.
Table A2 suggests that running our main specication on the subset of countries where no
simultaneous, confounding reforms are enacted, results in comparable treatment eect.
Table A2: Institutional Trust, accounting for simultaneous reforms.
Men Women
(1) (2) (3) (4) (5) (6)
Reform 0.021** 0.019 0.024** 0.010 0.011 0.015
(0.010) (0.012) (0.012) (0.009) (0.010) (0.011)
N. 7935 11796 17835 7906 12803 18599
Mean 0.37 0.37 0.36 0.37 0.37 0.36
Bandwidth 9 14 23 9 15 23
Country FE X X X X X X
ESS Wave FE X X X X X X
Notes.
p<0.10,∗ ∗ p<0.05,∗∗∗p<0.01
. We report here the estimates of the eect
of ending conscription on the rst component of a PCA between several forms of
trust. Coecients are estimated using a local linear regression, dierent polynomial
orders to construct the bias-correction, a triangular kernel function to construct the
local-polynomial estimator, and the standard Mean Squared Error optimal data-driven
bandwidth selector (see Calonico et al., 2017). Data for the main dependent and
independent variables come from
9
rounds of the European Social Survey (europeanso-
cialsurvey.org).
5
B Robustness to modelling choices
B.1 Alternative bandwidths
In Figure B2, we study the sensitivity of the estimated impact of the abolition of conscription on
institutional trust to dierent bandwidths, letting them vary between 2 and 15 years around the
threshold. We obtain consistently positive coecients across every specication: their magnitude
is greatest with a 3-years bandwidth, then declines and stabilizes as we expand the sample around
the threshold.
Figure B2: Institutional Trust by RD Bandwidth.
6
B.2 Alternative polynomial orders and kernel function
In this section, we report our coecients for varying polynomial orders, and test for the robust-
ness of our ndings to the adoption of a rectangular, rather than triangular, kernel in the RD
estimation. This specication weighs each observation equally, regardless of the distance from the
discontinuity, hence increasing the importance of observations further away from the threshold,
relative to when using a triangular kernel. The sign and magnitude of our treatment do not vary
substantially across the two specications (Table B3). This helps reassuring us that our estimates
are not driven by the positive (negative) views of respondents located immediately to the right
(left) of the threshold, who were born just late (not late) enough to avoid conscription.
Table B3: Institutional Trust: Triangular and Rectangular Kernel.
Triangular Kernel
Men Women
(1) (2) (3) (4) (5) (6)
Reform 0.026*** 0.022** 0.022** 0.008 0.007 0.009
(0.008) (0.009) (0.009) (0.007) (0.008) (0.008)
N. 12523 21059 30647 14792 21964 33031
Mean 0.37 0.37 0.36 0.37 0.37 0.36
Polynomial 1 2 3 1 2 3
Bandwidth 7 13 21 9 14 23
Rectangular Kernel
Reform 0.025*** 0.021** 0.029*** 0.008 0.004 0.011
(0.008) (0.009) (0.011) (0.006) (0.008) (0.009)
N. 9395 16899 22437 16249 19172 29413
Mean 0.37 0.37 0.37 0.37 0.37 0.36
Bandwidth 5 10 14 10 12 20
Polynomial 1 2 3 1 2 3
Country FE X X X X X X
ESS Wave FE X X X X X X
Notes.
p<0.10,∗ ∗ p<0.05,∗ ∗ ∗ p<0.01
. We report here the estimates of the eect
of ending conscription on the rst component of a PCA between several forms of trust.
Coecients are estimated using a local linear regression, dierent polynomial orders
to construct the bias-correction, a, resp., triangular/rectangular kernel function to con-
struct the local-polynomial estimator, and the standard Mean Squared Error optimal
data-driven bandwidth selector (see Calonico et al., 2017). Data for the main depen-
dent and independent variables come from
9
rounds of the European Social Survey
(europeansocialsurvey.org).
7
C Robustness to sampling choices
C.1 Alternative country sampling
Figure C3 demonstrates that our ndings are not driven by any single country. Indeed, the dierent
treatment eects obtained by deleting from the sample one country at a time - marked on the
right of gure C3 - are similar in magnitude and always statistically signicant at p<.05.
Figure C3: Institutional trust. Robustness to one-country deletion.
Notes. For each line, we delete the country indicated at the top of the gure. Each plot is obtained using the rdrobust package developed by
Calonico et al. (2017), based on IMSE-optimal binning and triangular dummy weights. 95% condence interval. Country and ESS-wave xed
eects apply.
8
C.2 Alternative unit sampling
In this section, we check whether our main results are robust to the re-inclusion in the sample of
individuals who completed tertiary education, which were dropped in our main analysis due to
concerns of potential conscription avoidance. Findings in Table C4 partly conrm our worries:
while we recover similar patterns as in the main paper, coecients for men appear to be slightly
weaker compared to our preferred specication, possibly due to higher average levels of trust
among more educated respondents.2
Table C4: Institutional Trust, including tertiary education.
Men Women
(1) (2) (3) (4) (5) (6)
Reform 0.011** 0.015* 0.014 0.003 0.003 0.004
(0.006) (0.008) (0.008) (0.005) (0.007) (0.007)
N. 22356 27912 37658 27608 31554 43572
Mean 0.38 0.38 0.38 0.38 0.38 0.38
Bandwidth 10 13 19 12 14 21
Polynomial 1 2 3 1 2 3
Country FE X X X X X X
ESS Wave FE X X X X X X
Notes.
p<0.10,∗ ∗ p<0.05,∗ ∗ p<0.01
. We report here the estimates of the
eect of ending conscription on the rst component of a PCA between several forms
of trust. Coecients are estimated using a local linear regression, dierent polyno-
mial orders to construct the bias-correction, a triangular kernel function to construct
the local-polynomial estimator, and the standard Mean Squared Error optimal data-
driven bandwidth selector (see Calonico et al., 2017). Data for the main dependent
and independent variables come from
9
rounds of the European Social Survey (euro-
peansocialsurvey.org).
2
In the replication material, we show how our results are robust to a dierent operationalization of the trust items,
i.e., recoding them as indicator variables taking value one if the level of trust is above 5 (zero otherwise).
9
C.3 Alternative reform dates
In order to test for the likelihood of our main nding to be spurious, we propose a randomization
test for the running variable. Specically, we randomize the date of each reform
1,000
times,
store the resulting randomized treatment eects, and calculate the share of replications producing
ndings that are similar to ours. Figure C4 demonstrates that our main nding is unlikely to be
spurious. Firstly, our actual treatment eect (marked with a green square in Subgure C4a) is
higher than any of the
1,000
ones obtained through the randomization (these are ordered from the
smallest to the largest for readability purposes). It is about
15%
higher than the highest random
treatment eect. Moreover, the share of cases in which a randomized discontinuity produces a
positive signicant eect on institutional trust is as low as
0.034
. Finally, the reader may note
that the average treatment eect across the 1,000 randomizations (marked with a violet square in
Subgure C4a), is
0.00047
- very close to the median replication - indicating that the distribution
of the random treatment eects is almost normal. Subgure C4b shows a similar picture. In
this case, it can be observed that our estimate is higher than the average across the randomized
treatment eects, yet not signicantly dierent from it. Overall, this test further increases our
condence in the internal validity of our ndings.
Figure C4: Institutional Trust: Random Reform Dates.
(a) Men (b) Women
Notes. Each plot is obtained using the rdrobust package developed by Calonico et al. (2017), based on IMSE-optimal binning and triangular dummy
weights. 95% condence interval. Country and ESS-wave xed eects apply.
10
C.4 Alternative trust measures
We show that the impact of the abolition of conscription on trust is very similar across legal system (top left of Table C.4), parliament (top
right), and parties (bottom left), whereas trust in politicians (bottom right) increases to a smaller extent.
Trust in Legal System Trust in Parliament
Men Women Men Women
(1) (2) (3) (1) (2) (3) (1) (2) (3) (1) (2) (3)
Reform 0.236** 0.227** 0.229** 0.048 0.052 0.050 0.258*** 0.228** 0.227** -0.004 -0.017 0.001
(0.093) (0.100) (0.108) (0.074) (0.090) (0.093) (0.091) (0.097) (0.104) (0.072) (0.089) (0.092)
N. 13965 23607 33168 18382 26392 40188 13899 23502 34276 18230 24669 38630
Mean 4.67 4.67 4.64 4.68 4.67 4.62 3.99 3.97 3.94 3.97 3.97 3.93
Bandwidth 7 13 20 10 15 25 7 13 21 10 14 24
Polynomial 1 2 3 1 2 3 1 2 3 1 2 3
Trust in Parties Trust in Politicians
Men Women Men Women
(1) (2) (3) (1) (2) (3) (1) (2) (3) (1) (2) (3)
Reform 0.200*** 0.183** 0.196** 0.065 0.050 0.063 0.131* 0.127 0.137 0.003 -0.016 -0.013
(0.077) (0.090) (0.094) (0.069) (0.085) (0.089) (0.072) (0.088) (0.090) (0.065) (0.080) (0.085)
N. 14302 22919 33442 16838 24126 35302 17391 25264 37011 20210 26646 40534
Mean 3.20 3.20 3.17 3.19 3.20 3.17 3.16 3.16 3.15 3.16 3.16 3.14
Bandwidth 8 14 23 10 15 24 9 14 23 11 15 25
Polynomial 1 2 3 1 2 3 1 2 3 1 2 3
Country FE X X X X X X X X X X X X
ESS wave FE X X X X X X X X X X X X
Notes.
p<0.10,∗ ∗ p<0.05,∗∗∗p<0.01
. We report here the estimates of the eect of ending conscription on several forms of trust. Coecients
are estimated using a local linear regression, dierent polynomial orders to construct the bias-correction, a triangular kernel function to construct the
local-polynomial estimator, and the standard Mean Squared Error optimal data-driven bandwidth selector (see Calonico et al., 2017). Data for the main
dependent and independent variables come from 9rounds of the European Social Survey (europeansocialsurvey.org).
D Analysis of Heterogeneity
D.1 Heterogeneity by graduality of conscription phaseout
In order to assess the extent of the measurement error arising from our eligibility-based intention
to treat, we collect qualitative data about the date of approval of each reform and quantitative
data about the number of conscripts in each of the sampled countries before the date in which
conscription formally ended.
Our main quantitative source for the number of conscripts is Military Balance (hereafter
MB
),
an authoritative database of military capabilities and security policy (see Strategic Studies and
Studies, 2020, for the 2020 issue). The MB annual reports date back to the early seventies, and
allow us to retrieve annual information about the number of conscripts for all of the sampled
countries but the Slovak Republic (for which no precise information is available following 2003)
and the United Kingdom (as the reform dates back to 1961). We complement the MB archive with
Eurostat data from the EU Labour Force Survey (hereafter
EU LF S
). The latter samples a large
number of households, providing detailed information on labour-market participation for people
aged 15 and over, as well as on people outside the labour force. We can thus retrieve the number
of individuals in each household that were conscripted at the time of interview. The EU-LFS is
useful for two reasons. First, it allows for an indirect cross-check of the quality of the MB data,
which relies on ocial sources. The correlation between the number of conscripts in the MB
database and the share of conscripts out of the total labour force according to EU-LFS is very
high (
ρ=0.93,p<0.001
), for the overlapping pool of years and countries (8 out of the 15 in our
sample), reassuring us about the accuracy of the MB data. Secondly, it allows us to provide an
overview of the drop in number of conscripts in the Slovak Republic. For the United Kingdom,
which is not covered by the EU-LFS either, we rely on data on the posting of national servicemen
to the armed forces from the British Ministry of Labour and National Service (dissolved in 1958,
after the abolition of conscription was approved), and retrieved by Vinen (2014).
Figure D5 provides evidence for two aggregate regularities that are important for our identi-
cation strategy. First, we can observe that the number of conscripts falls indeed to zero following
the intention to treat identied in our expanded version of Toronto (2007). This means that
our treatment group is indeed almost uniquely composed by individuals that were not drafted.
Secondly, Figure D5 indicates that, after the reform was approved (i.e., the year marked with
an hollow diamond on top of the corresponding bar), a large drop in the number of conscripts
can be observed in a majority of cases (see e.g., Subgures D5(a), D5(c)). In Portugal (Subgure
D5(j)), conscription is phased out rather slowly, and with an unclear pattern, whereas in the
Slovak Republic we observe a large drop in the number of conscripts even before the reform was
12
approved (D5(l)). In one case - Bulgaria (Subgure D5(b)) - the information is insucient to draw
strong conclusions.
While several EU countries ended conscription in the same year in which the relevant legislation
was approved, others chose to set a gradual phaseout period. We therefore collect from several
sources the date in which the law suspending conscription was rst passed, and compute the
distance from the year in which no voluntary army members were in place, according to our
amended version of the Toronto (2007) dataset. We retrieve the date of approval of most reforms
from War Resisters’ International (WRI), an international organization with headquarters in 40
countries that promotes peaceful international relationships, and has collected large qualitative
data about the approval of reforms intended to end conscription. Table D5 sums up the information
relative to each of these approval reforms, including the source and the law, typically promulgated
by the high chamber, that initiated the formal process of conscription phaseout.
Table D6 shows that the countries in which the reform was implemented sharply (i.e., the
distance between approval and completion was one year or less) display a 14.3% higher treatment
eect, according to our main specication. Furthermore, the larger eect in countries where the
reform was implemented more sharply likely reects stronger attitudinal homogenization among
conscripts, as discussed in the mechanisms section of the paper.
13
Figure D5: Active conscripts before and after conscription reforms.
(a) Source: Military Balance. (b) Source: Military Balance. (c) Source: Military Balance.
(d) Source: Military Balance. (e) Source: Military Balance. (f) Source: Military Balance.
(g) Source: Military Balance. (h) Source: Military Balance. (i) Source: Military Balance.
(j) Source: Military Balance. (k) Source: Military Balance. (l) Source: Military Balance.
(m) Source: Military Balance. (n) Source: Military Balance.
(o)
Source: Ministry of labour and
military service.
Notes. For each subgure, the vertical dashed line indicates the reform completion year, used in our analysis to split
the sample between treated and control units. The grey hollow diamond on top of one bar indicates the year in which
the conscription reform was approved. The number of dashed bars is therefore capturing policy graduality. Data
comes from the sources mentioned in the subcaption, with the exception of the datum for Germany in 2012, retrieved
from the country’s Central Oce for Foreign Education (ZAB), and the datum for Bulgaria in 2007, retrieved in the
WRI database.
Table D5: Reform Approval Dates (WRI, 2021, and other sources).
Country Approval Note (source: WRI, unless noted dierently) Other Sources (accessed 24/10/2021)
Belgium 1992 Conscription was suspended on 31 December 1992 by amending the 1962 Law on Conscription, which became applicable only to
conscripts drafted in 1993 and earlier. In practice this meant that the law no longer applied to those born in 1975 and later.
Manigart (2012)
Bulgaria 2006 Parliament approved a law on 24/06/2004 abolishing military conscription, paving the way for a fully professional army and ending a
feared rite of passage for young men in Bulgaria, a NATO member state. (New York Times, "Bulgaria Scraps the Draft", 29/06/2004)
https://nyti.ms/3GmfYxG
Czech
Republic
2004 Compulsory military service and substitute service for conscientious objectors have been abolished by an amendment to the Military
Act passed by the House of Deputies of the Parliament of the Czech Republic on 24 September 2004 and by the Senate on 4 November
2004.
France 1997 Loi n°97-1019 du 28 octobre 1997 portant réforme du service national. https://bit.ly/3Bdd2Qr
Germany 2011 In the reunited Germany it was maintained until 1 July 2011, and was suspended by the German parliament on 24 March 2011. https://bit.ly/3bnkgqF
Hungary 2004 The Law on Defence and the constitution have been changed on 4 November 2004 to abolish conscription. (...) The last 2,000 conscripts
were discharged from military service in November 2004. Since December 2004 the armed forces consist of professional soldiers only.
Italy 2000 The Senate in Rome approved measures agreed earlier this year by the lower house of parliament to phase out the military draft by
2006. (BBC News, "Italy abolishes the draft", 24/10/2000)
https://bbc.in/3pzIQg0
Netherlands 1992 After the end of the Cold War in 1989 the Meijer-committee started to investigate the matter again in 1991. After a one-year study the
committee concluded that conscription could not be abolished either. (...) Nevertheless, the Dutch parliament was of the opinion that
conscription had to be abolished. The government followed this opinion and stated that conscription should be ended at December 31,
1997. (Duindam, 1999, p.42)
Duindam (1999)
Poland 2009 Poland suspended compulsory military service on 5 December 2008 by the order of the Minister of Defence. Compulsory military
service was formally abolished when the Polish parliament amended the conscription law on 9 January 2009; the law came into eect
on 11 February 2009.
https://bit.ly/3vFQRRN
Portugal 1999 With Law 174/1999 (Law on Military Service, Lei do Serviço Militar), Portugal abolished conscription on 21 September 1999 and started
a transformation process into fully professional armed forces.
https://bit.ly/3zrF7nR
Slovak Repub-
lic
2005 Slovakia abolished conscription in 2005. (...) Presently, Slovakia maintains fully voluntary Armed Forces. However, Law No. 570/2005
Coll. on “National Service and on Change and Amendment of Some Acts” regulates conscription in times of crisis or war. The detailed
regulations are not known.
Slovenia 2002 Prime Minister Anton Rop and Defence Minister Anton Grizold have announced the nal abolishment of the mandatory military
service system in Slovenia, as recruits that were to start service in October will not be called in. (...) Grizold said that it would not be
expedient to keep this system until June 2004 - the latest possible date envisaged in the amendment to the military service act passed
in October 2002. (nato.gov.si, "Mandatory Military Service Abolished", 09/09/2003)
https://bit.ly/3vKEJiu
Spain 2001 El ministro de Defensa, Federico Trillo, pronunció el viernes una frase histórica: «Señoras y señores, se acaba la mili». El Gobierno ha
aprobado el decreto por el que se adelanta el n del servicio militar obligatorio al 31 de diciembre de 2001. (...) Precisamente, el último
sorteo del reemplazo del 2001 se celebró el 8 de noviembre del año pasado. (El Mundo, "Federico Trillo: «Señoras y señores, se acaba
la mili»", 11/03/2001)
https://bit.ly/3vHuYl0
Sweden 2009 Sweden on Thursday abolished a 100-year tradition of compulsory military service for men during peacetime, replacing it with a
voluntary system with rigorous requirements to join. The new policy means that required military service will be applied only if the
neutral Nordic nation of 9 million feels threatened. Lawmakers approved the change in a 2009 vote. (MSNBC, "Sweden scraps military
conscription", 01/07/2010)
https://bit.ly/2ZfWRV6
United
Kingdom
1957 It was generally known by 1957 that conscription was unlikely to be continued beyond 1960 (...). The Government’s intentions in
respect of future conscription were revealed in 1957. Its short-run objective was to build up the regular army and not to continue with
conscription beyond 1960. Plans were stated in a Command Paper, ‘Defence: Outline of Future Policy’ (Cmnd. 124, London, HMSO,
1957). See also Ministry of Labour Gazette, April 1957, pp. 123/4. (Grenet, Hart, and Roberts, 2011, p. 196)
Grenet, Hart, and Roberts (2011)
Table D6: Institutional Trust (1st and 2nd moment), by graduality of conscription phaseout.
Institutional Trust Institutional Trust (2nd Moment)
More than 1 Year More than 1 Year
Men Women Men Women
(1) (2) (3) (1) (2) (3) (1) (2) (3) (1) (2) (3)
Reform 0.021** 0.019 0.024** 0.010 0.011 0.015 -0.004 -0.006 -0.006 0.002 0.004 0.004
(0.010) (0.012) (0.012) (0.009) (0.010) (0.011) (0.005) (0.006) (0.006) (0.003) (0.005) (0.006)
N. 7935 11796 17835 7906 12803 18599 10290 15273 20898 17181 17896 21890
Mean 0.37 0.37 0.36 0.37 0.37 0.36 0.16 0.16 0.16 0.16 0.16 0.16
Bandwidth 9 14 23 9 15 23 12 19 28 21 22 28
1 Year or Less 1 Year or Less
Men Women Men Women
(1) (2) (3) (1) (2) (3) (1) (2) (3) (1) (2) (3)
Reform 0.024** 0.051** 0.055** 0.007 0.010 0.013 0.018*** 0.015 0.005 -0.003 -0.010 -0.016
(0.011) (0.020) (0.027) (0.011) (0.017) (0.034) (0.007) (0.010) (0.017) (0.007) (0.010) (0.015)
N. 6144 5435 6852 6290 6290 5624 5435 6144 6144 5624 5624 6290
Mean 0.37 0.37 0.37 0.37 0.37 0.37 0.16 0.16 0.16 0.16 0.16 0.16
Bandwidth 7 6 8 8 8 7 6 7 7 7 7 8
Polynomial 1 2 3 1 2 3 1 2 3 1 2 3
Country FE X X X X X X X X X X X X
ESS wave FE X X X X X X X X X X X X
Notes.
p<0.10,∗∗ p<0.05,∗∗∗p<0.01
. We report here the estimates of the eect of ending conscription on, resp., the rst component of a PCA between
several forms of trust, and its variance. Coecients are estimated using a local linear regression, dierent polynomial orders to construct the bias-correction,
a triangular kernel function to construct the local-polynomial estimator, and the standard Mean Squared Error optimal data-driven bandwidth selector (see
Calonico et al., 2017). Data for the main dependent and independent variables come from the European Social Survey (europeansocialsurvey.org).
D.2 Heterogeneity by reform date
Table D7 shows that treatment eects are stronger for more recent reforms (i.e., completed in 2004
or later), indicating how the eect of the end of conscription policies on trust-related attitudes
partly decays over time.
Table D7: Institutional Trust, by reform date (before/after 2004).
Before 2004
Men Women
(1) (2) (3) (4) (5) (6)
Reform 0.013 0.012 0.017 -0.011 -0.011 -0.007
(0.011) (0.013) (0.013) (0.010) (0.012) (0.013)
N. 6488 9725 15158 7013 10927 14464
Mean 0.37 0.37 0.36 0.37 0.37 0.36
Bandwidth 9 14 24 10 16 22
Polynomial 1 2 3 1 2 3
2004 or Later
Reform 0.029*** 0.043*** 0.051** 0.022 0.026 0.026
(0.010) (0.017) (0.022) (0.011) (0.016) (0.023)
N. 7364 7364 8964 6066 6955 7756
Mean 0.37 0.37 0.37 0.37 0.37 0.37
Bandwidth 7 7 9 6 7 8
Polynomial 1 2 3 1 2 3
Country FE X X X X X X
ESS Wave FE X X X X X X
Notes.
p<0.10,∗∗ p<0.05,∗∗∗p<0.01
. We report here the estimates of the eect of
ending conscription on the rst component of a PCA between several forms of trust. Co-
ecients are estimated using a local linear regression, dierent polynomial orders to con-
struct the bias-correction, a triangular kernel function to construct the local-polynomial
estimator, and the standard Mean Squared Error optimal data-driven bandwidth selector
(see Calonico et al., 2017). Data for the main dependent and independent variables come
from 9rounds of the European Social Survey (europeansocialsurvey.org).
17
D.3 Heterogeneity by socioeconomic background
Conscription may not have signicant overall eect on university enrollment as we pointed
out in the article, but it can nonetheless have heterogeneous eects which depend on the social
backgrounds of individuals (Di Pietro, 2013). To assess the impact of socio-economic backgrounds
in mitigating treatment eects, we subset on whether the respondents’ father and mother had
completed upper secondary education. Table D8 suggests that being born in a family where
the father is highly educated amplies the treatment eects, as we obtain signicantly larger
coecients. We do not recover a comparable pattern when looking at mothers’ education.
Table D8: Institutional Trust, by socioeconomic background.
Parents With Secondary Education
Mother Father
Men Women Men Women
Reform 0.020** 0.015 0.022* 0.009
(0.010) (0.009) (0.012) (0.010)
N. 8249 8215 15835 9722
Mean 0.37 0.37 0.36 0.37
Bandwidth 8 9 20 10
Parents Without Secondary Education
Mother Father
Men Women Men Women
Reform 0.019* -0.005 0.014 0.003
(0.010) (0.008) (0.010) (0.009)
N. 7733 11033 7671 9123
Mean 0.37 0.37 0.37 0.37
Bandwidth 11 15 12 14
Country FE X X X X
ESS Wave FE X X X X
Notes.
p<0.10,∗ ∗ p<0.05,∗∗∗p<0.01
. Coecients are esti-
mated using a local linear regression and a triangular kernel function
to construct the local-polynomial estimator, and the standard Mean
Squared Error optimal data-driven bandwidth selector (see Calonico
et al., 2017).
18
D.4 Heterogeneity by government ideology
Table D9 provides evidence that the ideology of the government in charge at the time of the reform
adoption - obtained from ParlGov data (Döring and Manow, 2021) - does not substantially alter
the eect of the abolition of conscription on institutional trust, neither per se, nor when matched
with the ideology of the executive in charge at the time of the interview.
Table D9: Institutional Trust, by government ideology.
Govt. Ideology at Adoption and Interview
Matching Not Matching
Men Women Men Women
Reform 0.023*** 0.005 0.025** 0.007
(0.009) (0.010) (0.011) (0.009)
N. 8424 6093 6595 8255
Mean 0.37 0.37 0.37 0.37
Bandwidth 14 10 6 8
Ideology of Govt. Approving Reform
Right-Wing Left-Wing
Men Women Men Women
Reform 0.021*** 0.013* 0.031** -0.000
(0.008) (0.008) (0.014) (0.011)
N. 11160 9925 3770 5647
Mean 0.37 0.37 0.37 0.37
Bandwidth 12 11 5 8
Country FE X X X X
ESS Wave FE X X X X
Notes.
p<0.10,∗ ∗ p<0.05,∗∗∗p<0.01
. Coecients are estimated
using a local linear regression and a triangular kernel function to construct
the local-polynomial estimator, and the standard Mean Squared Error
optimal data-driven bandwidth selector (see Calonico et al., 2017).
19
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