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Journal of Health Economics 42 (2015) 186–196

Contents lists available at ScienceDirect

Journal of Health Economics

jo u r n al homep age: www.elsev ier .com/ locate /econbase

obacco control campaign in Uruguay: Impact on smoking cessationuring pregnancy and birth weight

effrey E. Harrisa,∗, Ana Inés Balsab, Patricia Triunfoc

Department of Economics, Massachusetts Institute of Technology, Cambridge, MA 02139, USADepartamento de Economía, Facultad de Ciencias Empresariales y Economía, Universidad de Montevideo, Montevideo 11500, UruguayDepartamento de Economía, Facultad de Ciencias Sociales, Universidad de la República, Montevideo 11200, Uruguay

r t i c l e i n f o

rticle history:eceived 23 April 2014eceived in revised form 13 April 2015ccepted 20 April 2015vailable online 29 April 2015

EL classification:181212

a b s t r a c t

We analyzed a nationwide registry of all pregnancies in Uruguay during 2007–2013 to assess the impact ofthree types of tobacco control policies: (1) provider-level interventions aimed at the treatment of nicotinedependence, (2) national-level increases in cigarette taxes, and (3) national-level non-price regulationof cigarette packaging and marketing. We estimated models of smoking cessation during pregnancy atthe individual, provider and national levels. The rate of smoking cessation during pregnancy increasedfrom 15.4% in 2007 to 42.7% in 2013. National-level non-price policies had the largest estimated impacton cessation. The price response of the tobacco industry attenuated the effects of tax increases. Whileprovider-level interventions had a significant effect, they were adopted by relatively few health centers.Quitting during pregnancy increased birth weight by an estimated 188 g. Tobacco control measures had

eywords:conomic evaluationigarette taxesackage warningsdvertising bansobacco control

no effect on the birth weight of newborns of non-smoking women.© 2015 Elsevier B.V. All rights reserved.

. Introduction

The tobacco epidemic continues to represent a serious publicealth threat throughout the world. By one recent estimate, theorldwide annual mortality burden has already reached 5 millioneaths from direct tobacco smoking and another 600,000 deathsttributable to the effects of environmental smoke (World Healthrganization, 2012). Within the next 20 years, annual deaths from

obacco are projected to continue to rise to 8 million, of which morehan 80% will occur in low- and middle-income countries (Matherst al., 2008).

Beginning in 2005, Uruguay instituted a series of aggressive anti-moking measures that placed this small South American country

f 3.3 million inhabitants in the forefront of tobacco control policyorldwide. By 2012, the Uruguayan government had prohibited

moking in enclosed public spaces and workspaces, banned nearly

∗ Corresponding author. Tel.: +1 617 253 2677; fax: +1 617 253 6915.E-mail addresses: jeffrey@mit.edu (J.E. Harris), abalsa@um.edu.uy (A.I. Balsa),

atricia.triunfo@cienciassociales.edu.uy (P. Triunfo).

ttp://dx.doi.org/10.1016/j.jhealeco.2015.04.002167-6296/© 2015 Elsevier B.V. All rights reserved.

all advertising and promotion of tobacco products, mandated thatpictograms with warnings cover 80% of the front and back ofevery pack, banned misleading marketing terms such as “light” and“mild,” and outlawed multiple versions of the same brand such asSilver or Blue. Tobacco taxes were increased, and all healthcareproviders were required to offer treatment for nicotine depend-ence.

In a previous report, two of us (JH and PT) found that Uruguay’scomprehensive nationwide antismoking campaign was associatedwith a substantial, unprecedented decrease in tobacco use (Abascalet al., 2012). During 2005–2011, per capita cigarette consumptiondecreased by 4.3% per year, while the 30-day prevalence of cigaretteuse among students aged 13–17 years and the overall populationprevalence of current tobacco use declined at annual rates of 8.0%and 3.3%, respectively. The observed declines in each of these threeindicators of tobacco use were significantly larger than those seenin neighboring Argentina, a culturally similar country that had not

conducted a comprehensive antismoking campaign and served asa control.

While our previous study contributed to the evaluation ofthe overall impact of Uruguay’s tobacco control campaign, it did

alth E

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In 2008, the comprehensive tobacco control law mandated thatevery primary care provider, whether public or private, incorporate

1 This “80% rule” was promulgated 3 months before the issuance of the fourthround of images. However, we have no evidence of significant compliance with the80% rule before the deadline for compliance with the fourth round of images.

2 With the exception of the comprehensive tobacco control law, all measuresprovided for a 180-day compliance period. By specifying the end of the compliance

J.E. Harris et al. / Journal of He

ot address the quantitative contributions of individual campaignomponents. Pursuing that objective here, we classify the inter-entions implemented in Uruguay during 2007–2013 into threeategories: (1) provider-level interventions aimed at the treatmentf nicotine dependence, (2) national-level increases in cigaretteaxes, and (3) national-level non-price regulation of cigarette pack-ging and marketing. We study the effects of these individualampaign components on a critical target population – pregnantomen.

Studying the population of pregnant women is important notnly for the well-recognized adverse health consequences ofmoking during pregnancy (Permutt and Hebel, 1989; da Veigand Wilder, 2008; McCowan et al., 2009), but also for the nar-ow nine-month window during which pregnant women haveeightened susceptibility to health-related interventions. We takedvantage of a continuous nationwide registry of all live preg-ancies from 2007 to 2013 to study the effects of the campaignn two main outcomes: the probability that a pregnant smokerill quit smoking by her third trimester and her infant’s birtheight.

To identify the effect of the provider-level interventions, wese a difference-in-differences (DID) approach, exploiting the facthat these policies were implemented at different health centerst different times. To assess the effect of taxes, we rely upon aeries of discrete tax increases during our study period. Finally, tossess the effects of non-price regulation of packaging and market-ng, we take advantage of the fact that these nationwide measures

ent into effect at different times. As an additional control, weompare the effect of these interventions on the birth weight ofhildren whose mothers smoked during pregnancy with the cor-esponding effect, if any, on the offspring of mothers who did notmoke.

Our study contributes to an extensive literature evaluatinghe impact of such tobacco control policies as tax increases,ontrol of environmental tobacco smoke, cigarette pack war-ings, restrictions on cigarette marketing, regulation of tobaccoonstituents, mass media anti-smoking campaigns, and the treat-ent of addiction (Saffer and Chaloupka, 2000; Wakefield and

haloupka, 2000; Powell et al., 2005; Blecher, 2008; Carpenter andook, 2008; DeCicca et al., 2008; Anger et al., 2011; Hammond,011; Hoek et al., 2011; Chaloupka et al., 2012; Emery et al.,012; Mons et al., 2013). Our work is distinguishable in thate exploit an extensive micro database to evaluate the relative

mpacts of multiple types of interventions in the context of aationwide tobacco control campaign conducted in a developingountry.

We find persuasive evidence on the impact of each of the threeolicy categories analyzed – provider-level interventions, taxes,nd non-price policies – on the likelihood of quitting smokinguring pregnancy and on birth weight. In terms of the relativeontributions of each of these policies to the observed increasen quit rates, the regulation of marketing and packaging had thetrongest effect, accounting for 71% of the total observed varia-ion in quit rates during 2007–2013. While interventions to treaticotine dependence had a strong effect at the level of the indi-idual provider, relatively few prenatal care centers adopted thesenterventions during the study period, thus contributing little tohe overall increase in the quit rate. Tax increases, on the otherand, explained an estimated 25% of the variation in quit rates dur-

ng 2007–2013. While real taxes increased 122% during that time,he tobacco-industry passed on only a fraction of the tax increaseso consumers, so that real cigarette price increased by only 17%.inally, we find that smoking cessation was associated with a sig-ificant increase in birth weight. By contrast, the tobacco control

olicies under study had no effect on the birth weight of offspringf mothers who did not smoke.

conomics 42 (2015) 186–196 187

2. Background and data

2.1. Nationwide anti-smoking policies

In 2005, one year after the legislature had ratified the Frame-work Convention on Tobacco Control, Uruguay’s newly electedadministration launched a National Program for Tobacco Controlthat formed the basis for a succession of progressively more strin-gent tobacco control policies (Abascal et al., 2012). In March 2006,all enclosed public spaces and all public and private workspaceswere declared 100% smoke-free. In June 2008, the scope of tobacco-free spaces was extended to taxis, buses, airplanes and other publictransport.

These curbs on environmental tobacco smoke were paralleledby a series of advertising restrictions on tobacco products. In May2005 the government banned cigarette advertising on televisionduring children’s viewing hours (before 9:30 pm) and prohibitedadvertising, promotion or sponsorship by tobacco companies of allsporting events. These restrictions were subsequently codified inMarch 2008, when comprehensive tobacco control legislation (Law18.256) prohibited all advertising and promotion of tobacco prod-ucts except at point of sale. In October 2008, logos, trademarks andother tobacco-related symbols were banned on non-tobacco prod-ucts. In May 2014, all advertising was prohibited, even at the pointof sale.

In addition, the Uruguayan government promulgated warningrequirements on cigarette packages and imposed restrictions onmanufacturers’ branding practices. A May 2005 ministerial decreebanned all references to “light,” “ultra light,” “mild,” “low tar” andother descriptors that might misleadingly imply reduced harm. Thedecree also mandated a series of rotating warnings with imagescovering 50% of the front and back of each cigarette pack. Thedeadline for compliance with the first round of these rotating war-nings was April 2006. Subsequent rounds had respective deadlinesof December 2007, February 2009, February 2010, January 2012,and April 2013. A “single presentation rule,” issued as a minis-terial decree along with the third round of warnings, barred themarketing of multiple versions of the same brand, such as Silveror Blue. Finally, a 2009 decree mandated that the size of the war-nings be increased to 80% of the front and back of each pack. Thisrequirement was implemented with the fourth round of warningsand became effective by February 2010.1

Fig. 1 shows a timeline summarizing the major nationwidenon-price regulatory measures from 2005 to 2013. The blue textdescribes each of the six rounds of package warnings, while theboldface red text describes regulatory measures other than themandated warnings. The black lines point to the compliance dead-lines for each regulatory measure.2

Fig. 2 further describes the six rounds of rotating package war-nings. In each round, we show only one of several mandated images.The relative sizes of the images in the figure correspond to their rel-ative sizes on each pack, with the last three rounds reflecting therequired increase from 50% to 80% of the front and back surfaces.

2.2. Smoking cessation programs directed at healthcare providers

period as the effective date of each measure, we assumed that tobacco manufactur-ers waited until each deadline to comply.

188 J.E. Harris et al. / Journal of Health Economics 42 (2015) 186–196

2005

Smoking prohibitedin all enclosed publicspaces and all public

and private work spaces.

1st round ofpackage warnings.

Warnings must cover50% of both front & back.

2nd round ofpackage warnings.

3rd round ofpackage warnings.Brands restricted toa single presentation .

4th round ofpackage warnings.Warnings must cover80% of both front & back.

5th round ofpackage warnings.

6th round ofpackage warnings.

Comprehensive tobaccocontrol legislation.

All advertising exceptpoint-of-sale banned.

2006 2007 2008 2009 2010 2011 2012 2013 2014

F efers

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Fr

ig. 1. Timeline of nationwide non-price tobacco control measures. The blue text roldface red text refers to other tobacco control measures.

he diagnosis and treatment of tobacco dependence into its menuf basic services. Pursuant to this legislation, in 2009 the Ministryf Public Health and the National Resource Fund (“Fondo Nacionale Recursos” or FNR), the governmental agency responsible fornancing resource-intensive medical technologies, establishedational guidelines for primary care providers on the diagnosisnd treatment of nicotine dependence. Through a set of agree-ents (“convenios”) with the FNR, healthcare institutions were

ligible to receive training and free nicotine patches and bupro-ion in return for setting up a smoking cessation program with

ittle or no patient copayments (Esteves et al., 2011). Health

ig. 2. Timeline of six rounds of rotating package warnings. Each round displays only onelative sizes on each pack, with the last three rounds reflecting the required increase fro

to the deadlines for each of the six rounds of rotating package warnings, while the

centers that had no agreements with the FNR were requiredto provide smoking cessation services in accordance with theguidelines, but they were permitted to charge nontrivial copay-ments to patients. In what follows, we refer to these agreementsbetween health centers and the FNR as “provider-level agree-ments.”

Among all sites providing prenatal care to pregnant women, theproportion with FNR agreements increased from 7 to 12% during

2005–2013. Concurrently, the proportion of all pregnant womenreceiving prenatal care at sites with FNR agreements increased from13% in 2005 to 36% in 2007, but then declined to 31% by 2013.

e of several mandated images. The relative sizes of the images correspond to theirm 50% to 80% of the front and back surfaces.

J.E. Harris et al. / Journal of Health Economics 42 (2015) 186–196 189

Real Price

Real Taxes(Excise + VAT)

010

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6070

80

2001 2003 2005 2007 2009 2011 2013

Year

(Bas

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Dec

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Uru

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ayan

Pes

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per

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A B C D E F G H

Fig. 3. Real price and real taxes per pack of cigarettes, 2001–2013. The vertical lines show the timing of non-price nationwide policy measures, as described in Fig. 1.(A) Smoking prohibited in all enclosed public spaces and all public and private workspaces. (B) 1st round of package warnings. (C) 2nd round of package warnings. (D)C ds resc ckage

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from this new system, which we refer to as the “new SIP,” were thefocus of our analysis.

omprehensive tobacco control legislation. (E) 3rd round of package warnings; branover 80% of front and back. (G) 5th round of package warnings. (H) 6th round of pa

.3. Cigarette tax increases

In addition to the foregoing policy interventions, the Uruguayanovernment increased its indirect taxes on tobacco products.mposed solely at the national level, these taxes consist of anxcise tax (“impuesto específico interno” or IMESI) and a valuedded tax (“impuesto al valor agregado” or IVA). The IMESI, whichas first applied to cigarettes in 1993, underwent a series of dis-

rete increases in June 2002, May 2003, July 2007, June 2009, andebruary 2010. The IVA, by contrast, was first applied to cigarettesn July 2007 and since then has constituted 22% of the pre-taxrice including the IMESI or, equivalently, 18% of the retail price.ig. 3 shows the estimated real price and real tax on a pack ofigarettes during 2001–2013. Only 45% of the abrupt increase inigarette taxes in July 2007 was passed on to consumers in theorm of higher retail prices. The construction of the real pricend tax series is described in our working paper (Harris et al.,014).

In Uruguay, an estimated 99% of tobacco users smoke manu-actured cigarettes, hand-rolled cigarettes, or both (Abascal et al.,012). Manufactured cigarettes, in particular, make up morehan 85% of taxable cigarette consumption (Dirección Generalmpositiva, 2012). During 2004–2012, by one estimate, contrabandigarette sales constituted approximately 12% of total cigaretteonsumption on average (Curti, 2013). With the possible excep-ion of less densely populated provinces (“departamentos”) alongruguay’s borders with Brazil and Argentina, where contraband

obacco use appears more prevalent, there has been little effectiveeographical variation in retail price.

.4. Perinatal information system (SIP)

Our source of micro data on the smoking practices of pregnantomen was the Perinatal Information System (“Sistema Infor-ático Perinatal” or SIP), a mandatory nationwide electronic

egistry operating in all prenatal care clinics in Uruguay since 1990.eveloped and overseen by the Latin American Center for Peri-atology (“Centro Latinoamericano de Perinatología” or CLAP) ofhe Pan American Health Organization, the database contained

tricted to a single presentation. (F) 4th round of package warnings; warnings must warnings.

information at the level of the individual pregnancy on maternalcharacteristics, self-reported smoking behavior, current and pastobstetric history, the timing of prenatal care, the sites of prenatalcare and delivery, and birth outcomes including birth weight (CLAP,2001). In 2012, the SIP covered an estimated 94% of all live birthsin Uruguay.

Our analyses relied upon the following individual-level mater-nal characteristics, derived from the SIP registry: the timing ofthe first prenatal visit (first-trimester prenatal care); the mother’sage (<16, 17–19, 20–34, 35–39, and 40+ years), marital status(single, married, cohabiting, other), and educational attainment(primary, secondary, university); the number of prior deliveries(0, 1, 2, 3, 4+); number of prior abortions; a history of diabetesor hypertension; whether any complications of pregnancy wereobserved, in particular, the presence of preeclampsia or eclamp-sia; the mother’s body mass index based on her self-reportedheight and weight prior to the pregnancy (underweight, normalweight, overweight, obese); the mother’s use of alcohol or illicitdrugs; the sites of prenatal care; and the newborn’s sex and birthweight.3

Prior to 2007, each individual record in the SIP database con-tained the pregnant woman’s smoking status only at the time ofinitiation of prenatal care. It did not show changes in smoking, ifany, during the course of her pregnancy. Under a new data entrysystem beginning in 2007, the prenatal record noted the woman’ssmoking status separately in each trimester of her pregnancy. Forexample, if a woman initiated prenatal care in her second trimester,the healthcare provider recorded her smoking status in the firsttrimester, based on her recall, as well as in the current trimester.Her smoking status would subsequently be recorded in a follow-upprenatal visit during her third trimester. The perinatal data derived

3 To avoid loss of observations, we included dummy variables equal to 1 whensome maternal characteristics were missing. For further details on maternal andpregnancy characteristics, including descriptive statistics, see our working paper(Harris et al., 2014).

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tax per pack was 0.079 (p = 0.031). At the sample mean valueof the dependent variable equal to 0.377, the estimated elastic-ity of the smoking cessation with respect to cigarette taxes was

4 For the individual-level model of Eq. (1), we assigned a woman to calendar date

90 J.E. Harris et al. / Journal of He

. Principal endpoints: smoking cessation and birth weight

To assess the impact of Uruguay’s tobacco control campaign, weocused our attention primarily on pregnant women who smokedigarettes at any time from the first prenatal visit onward. Withinhis target group of pregnant smokers, our principal endpointas smoking cessation by the third trimester. Our analysis of

his endpoint was confined to the interval from 2007 to 2013,hen data on smoking habits during each trimester were avail-

ble through the new SIP system. Fig. 4 shows the progressivencrease in the annual mean quit rate among pregnant smokersrom 15.4% in 2007 to 42.7% in 2013. Our main research objec-ive was to determine what proportion of this substantial rise inuit rates could be attributed to Uruguay’s multi-component cam-aign.

Why did not we focus on the prevalence of smoking at the onsetf pregnancy? Unfortunately, within the limitations of Uruguay’sIP system, this alternative endpoint was subject to a critical sourcef potential measurement bias. Starting in July 2008, the Uruguayaninistry of Health established a new system of financial incentives

or providers to increase the completeness of data reporting on SIPecords. As Fig. 5 shows, the prevalence of smoking at the firstrenatal visit remained stable at about 25% from 2000 to 2005.hereafter, with the onset of the tobacco control campaign, therevalence had declined toward 15% by the early months of 2009.

n April 2009, however, nine months after the institution of the newystem of financial incentives, the prevalence abruptly increased.t the same time, as shown in Fig. 5, the proportion of records withissing data declined dramatically from about 20% in 2009 to 1–2%

y 2013.The best explanation for the abrupt break in prevalence is

hat women with missing data on smoking at the onset ofregnancy were more likely to be smokers. Moreover, as theinistry of Health imposed increasingly strict goals for data com-

leteness, the effect of including these previously unreportedmokers in the prevalence calculation is likely to have grownver larger. While we did have some data on the Ministry’sata-completeness goals, we concluded that the task of correct-

ng for this missing data bias and at the same time identifyinghe effects of post-2009 tobacco control measures would proventractable.

On the other hand, we did not detect any comparable break inhe monthly time series of smoking cessation rates. We thus con-idered the quitting to be a more reliable and sensitive endpointhan smoking prevalence. Still, to the extent that the new systemf data-completeness goals recorded an increasing number of hard-ore smokers, our estimates in Fig. 5 of quit rate during 2009–2013ould be biased downward. We stress that our principal endpoint

epresents the rate of cessation conditional upon smoking on orfter the first prenatal visit.

Smoking cessation during pregnancy is known to reduce itsdverse health effects. Accordingly, as an additional endpoint, wetudied the impact of Uruguay’s tobacco control campaign onirth weight. As shown in Fig. 6, the difference in birth weightetween non-smokers and continuing smokers was on the order of10 g, while the corresponding difference between non-smokersnd quitters was only about 25 g. Although the smaller numberf quitters in the SIP database during 2007–2008 decreased therecision of the mean birth weight estimates, Fig. 6 still shows aackground increase in birth weight for all three groups. The anal-sis of birth weight also helped us address the concern that the SIPegistry contained self-reported data on smoking habits. If womenad falsely reported having quit smoking with increasing frequencys the campaign progressed, we would have expected to see a grow-

ng reduction in the apparent favorable effects of cessation on birth

eight.

conomics 42 (2015) 186–196

3.1. Impact on quitting during pregnancy

3.1.1. Individual-level analysisWe first investigate the effect of the provider-level agreements

and national-level tobacco control policies on the quit rate duringpregnancy. To that end, we begin with a linear probability modelbased upon observations at the level of the individual pregnantwoman:

yist = c′i˛0 + x′

st˛1 + z′t˛2 + Ds + eist (1)

where the subscript i indexes each woman, the subscript s refersto the health center where she received prenatal care, and the sub-script t refers to the calendar date corresponding to the midpointof her third trimester.4 The data yist are binary variables repre-senting smoking cessation, where yist = 1 if the woman quit andyist = 0 if she continued to smoke through her third trimester. Thevector of exogenous variables ci represents individual-level mater-nal characteristics, while xst represents the presence or absence ofa provider-level agreement at health center s on calendar date t,and the vector zt represents those national-level policy variablesincluding cigarettes taxes that were in effect at calendar date t. Theparameters Ds represent health center-specific fixed effects. Weassume that the unobserved error terms eist are uncorrelated withthe observed explanatory variables and have zero means.

Since the presence or absence of a provider-level agreementxst varied by health center and calendar date, the impact of theseprograms was identifiable via a DID model. With respect to thenational-level policies zt, however, we needed to be careful aboutwhat policy impacts could and could not be identified from thedata. Successive increases in cigarette taxes during the 2007–2013observation period, beginning with the inclusion of tobacco in thevalue-added tax on July 1, 2007 (Fig. 3), permitted us to identifythe impact of this policy. On the other hand, we could not iden-tify the impacts of the two non-price policies that went into effectbefore the start of our observation period: the prohibition of smok-ing in public places and enclosed workspaces (March 1, 2006) andthe requirement that all packs contain rotating images with war-nings covering 50% of the front and back of each pack (April 18,2006). Moreover, the effective dates of the second, third and fourthrounds of warnings were either close to or coincident with otherpolicy measures, and thus their impacts could not be separatelyidentified without additional strong assumptions concerning theireffects over time (Fig. 1).

That left us with five non-price, national-level policies: the com-prehensive tobacco legislation banning nearly all advertising (ineffect from March 6, 2008 onward); the single presentation rule (ineffect from February 14, 2009 onward); the increase in the warningsize from 50% to 80% of the front and back of each pack (in effectfrom February 28, 2010 onward); the fifth round of warnings (ineffect from January 7, 2012 through April 7, 2013); and the sixthround of warnings (in effect from April 8, 2013 onward).

Column (A) of Table 1 shows our results. We estimated theparameters of Eq. (1) by ordinary least squares (OLS) with Huber-White robust standard errors implemented at the individual level.The presence of an agreement between the woman’s health centerand the FNR increased the probability of quitting by an esti-mated 4.8 percentage points (p = 0.024). The coefficient of the log

t based on the midpoint of her prenatal care visits during her third trimester ofpregnancy. If she had no prenatal visits, we assigned her a date t equal to 30 daysprior to delivery.

J.E. Harris et al. / Journal of Health Economics 42 (2015) 186–196 191

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Year of Midpoint of Third Trimester

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ig. 4. Increase in mean quit rate among pregnant smokers, 2007–2013. Vertical bamokers in the SIP database with data on smoking status in the third trimester. Earenatal visits.

.079/0.377 = 0.21. All five of the non-price nationwide policiesad significant effects, with the comprehensive tobacco control

aw assuming the dominant role. All five non-price policies com-ined increased the probability of quitting by an estimated 26.9ercentage points (p < 0.001).

We used the results of our individual-level analysis to com-ute the relative contributions of each of the three categories ofobacco control policy to the overall change in smoking cessa-ion rates observed during the 2007–2013 study period. To thatnd, we first computed the predicted values yist derived from Eq.1) and then calculated the corresponding sum Y =

∑i,s,t yist over

ll observations. We then recomputed the predicted values yist

nd corresponding sums Y , successively setting all values of therovider-level agreement variable xst equal to 0, then all values ofhe log real tax rate equal to the initial level in January 2007, and

05

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30

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of

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oki

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at F

irst

Pre

nat

al V

isit

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% Missing Data

Month of B

ig. 5. Monthly prevalence of smoking at the first prenatal visit. Monthly proportion of

he proportion with missing data is measured on the right. The diameter of each data poi

resent 95% confidence intervals. Adjacent to each point is the number of pregnantoker was assigned to the calendar year of the mean date of all her third-trimester

then all indicators of non-price policies zt equal to 0. Based on thisdecomposition procedure, we estimated the following attributableproportions: provider-level agreements, 4.3%; tax increases, 25.2%;and regulations of packaging and marketing, 70.5%.

3.2. Health center level analysis

It is arguable that an individual-level analysis of Eq. (1) over-states the precision of estimated policy impacts. The central thrustof this criticism is that the agreements for smoking cessation ser-vices were made with health centers rather than with individual

patients. Moreover, the tax increases and non-price policies werecarried out at the national rather than the individual level. Toaddress these concerns, we performed a series of aggregate anal-yses at both the health center level and national level. Following

05

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Pro

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Dat

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records with missing data. Smoking prevalence is measured on the left axis, whilent is proportional to the number of observations.

192 J.E. Harris et al. / Journal of Health Economics 42 (2015) 186–196

3000

3100

3200

3300

3400

Bir

th W

eig

ht

(gm

)

2007 2008 2009 2010 2011 2012 2013

Year of Birth

95% CI

Smokers Who Quit

Non-Smokers

Continuing Smokers

Fig. 6. Annual mean birth weight among non-smoking pregnant women, continuing smokers, and smokers who quit, 2007–2013. Non-smokers were pregnant women whodid not report smoking at any prenatal visit. Continuing smokers were pregnant women who reported smoking at one or more prenatal visits, but had not quit smoking bythe third trimester. Smokers who quit likewise reported smoking at one or more prenatal visits, but had quit by the third trimester.

Table 1Estimated effects on probability of quitting by the third trimester of pregnancy.

Independent variable (A) (B) (C) (D) (E)

Provider-level agreements 0.048** (0.021) 0.056* (0.034) 0.056** (0.025) 0.056** (0.025)Log real tax per pack 0.079** (0.036) 0.106** (0.053) 0.105* (0.054) 0.136** (0.055)Tobacco control law 0.094*** (0.017) 0.138*** (0.038) 0.138*** (0.026) 0.139*** (0.023)Single presentation rule 0.075*** (0.014) 0.053** (0.023) 0.053*** (0.019) 0.039** (0.015)80% rule 0.028*** (0.011) 0.029* (0. 015) 0.030* (0.015) 0.032* (0.016)Fifth round of warnings 0.037*** (0.008) 0.030*** (0.011) 0.030*** (0.011) 0.036*** (0.007)Sixth round of warnings 0.035*** (0.011) 0.0355** (0.0147) 0.035** (0.015) 0.038*** (0.010)Five non-price measures combined 0.269*** (0.020) 0.286*** (0.044) 0.285*** (0.027) 0.283*** (0.022)No. observations 31,230 1422 1400 1400 28

* Significant at p < 0.10.** Significant at p < 0.05.

*** Significant at p < 0.01.A. OLS estimation on individual maternal-level observations, based on Eq. (1). White-Huber robust standard errors. Coefficients of individual maternal characteristics andhealth center fixed effects not shown.B. OLS estimation on observations grouped by health center and calendar quarter, based on Eq. (3). Standard errors adjusted for clustering at level of health center. Observationsweighted by inverse of standard errors of fixed effects derived from Eq. (2).C. FGLS estimation on observations grouped by health center and calendar quarter, based on Eq. (3). Standard errors adjusted for clustering at level of health center. Uniformfirst-order serial correlation estimated to equal 0.0210. Observations weighted by inverse of standard errors of fixed effects derived from Eq. (2).D. FGLS estimation on observations grouped by health center and calendar quarter, based on Eq. (3). Standard errors adjusted for clustering at level of health center. Uniformfi nverseE 4). NeO q. (2).

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health center s and calendar quarter t of a pregnant smoker inthe reference category of maternal characteristics.5 We then esti-mated the parameters of the DID model (3), where the dependent

rst-order serial correlation estimated to equal 0.0237. Observations weighted by i. OLS estimation on observations grouped by calendar quarter, based upon Eq. (bservations weighted by inverse of standard errors of fixed effects derived from E

Amemiya, 1978; Hansen, 2007; Imbens and Woolridge, 2014) andthers, we specified the following two-stage model.

ist = c′iˇ0 + Fst + uist (2)

st = x′stˇ1 + z′

tˇ2 + Gs + vst (3)

Here, the subscript s = 1, . . ., S continues to index health centers,hile the subscript t = 1, . . ., T now indexes calendar quarters. The

ubscript i = 1, . . ., Nst now indexes women who received prena-al care at health center s and whose third trimester occurred inalendar quarter t.

In the first stage (Eq. (2)), the data yist are binary variables repre-enting smoking cessation and the exogenous variables ci represent

ndividual-level maternal characteristics, while Fst are fixed effectsor each of the ST combinations of health center and calendar quar-er. In the second stage (Eq. (3)), the data xst represent the presencer absence of a provider-level agreement at health center s during

of standard errors of fixed effects derived from Eq. (2).wey-West standard errors adjusted for heteroskedasticity and serial correlation.

calendar quarter t, while the data z′t denote the national-level poli-

cies in effect in calendar quarter t. The parameters Gs are S healthcenter-specific fixed effects. We assumed that the unobserved errorterms uist and vist were uncorrelated with the observed explanatoryvariables and with each other, and had zero means.

To estimate the model parameters, we first ran OLS on Eq.(2), thus obtaining estimates Fst of the parameters Fst. In effect,these OLS estimates represented the predicted quit rate in each

5 A woman in the reference category was married, aged 20–34 years, had lessthan a high school education, did not seek prenatal care in her first trimester, hadno prior abortions or deliveries, a pre-pregnancy body mass index 18.5–24.9 kg/m2,no history of diabetes, hypertension, eclampsia or pre-eclampsia, and gave birth to

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ariable Fst was replaced by its estimated value Fst . We weighted thebservations by the inverse of the standard errors of the estimates

ˆst .Within the context of this aggregate model, researchers have

xpressed concerns that traditional OLS estimation of DID modelsgnores serial correlation of errors and thus overstates the precisionf the coefficient estimates (Bertrand et al., 2004; Cameron et al.,008). In our context, serial correlation would arise when healthenters were subject to common unobserved shocks that per-isted for more than a calendar quarter. To address these concerns,e estimated the parameters of Eq. (3) by feasible generalized

east squares (FGLS) under varying specifications of the covarianceatrix V = E[vstvs′t′ ].Columns (B) and (C) in Table 1 show our regression estimates of

he parameters ˇ1 and ˇ2 of Eq. (3) under two different assump-ions concerning the covariance matrix. In column (B), we assumedlustering of errors within each health center. In column (C), wessumed first-order temporally correlated errors with a uniformorrelation coefficient among health centers. We found quite simi-ar results when we estimated Eq. (3) under the assumption that theoefficient of serial correlation varied by health center (not shownn Table 1). In comparison with the maternal-level estimates (col-mn A), we observed larger coefficients for two policies: the log realigarette tax and the comprehensive tobacco control law. However,heir corresponding standard errors were also increased, so that weould not reject the hypothesis that their impacts equalled thosestimated at the individual-level data. Finally, in both columns (B)nd (C), the combined effect of the five non-price policies was indis-inguishable from the effect estimated from individual-level data.

.3. National level analysis

It is arguable that the 2-stage model of Eqs. (2) and (3) stillverstates the precision of the estimated impacts of cigarette taxesnd non-price regulations of cigarette packaging and marketing,s these policies were carried out at the national level. To addresshis criticism, we extended our two-stage model of Eqs. (2) and3) to three stages. In particular, we continued to specify the first-tage model of Eq. (2), but replaced Eq. (3) with the following twoquations:

st = x′st�1 + Hs + Jt + �st (4)

t = z′t�2 + �t (5)

As before, we assumed that the unobserved error terms in (2),4) and (5) were uncorrelated with their respective explanatoryariables.

The second-stage Eq. (4) differs from (3) in that Fst now dependsn the presence or absence of a provider-level agreement xst atealth center s during calendar quarter t, as well as health centerxed effects Hs, calendar quarter fixed effects Jt, and an unobservedandom error �st with mean zero. To estimate the policy impactarameters �1 in (4), we replaced the fixed effects Fst with theirstimates Fst from Eq. (2). As in the two-stage model, Eq. (4) wasstimated by feasible GLS under various assumptions concerninghe covariance matrix of the errors, where the observations wereeighted by the inverse of the standard errors of the estimates Fst .

In third-stage Eq. (5), the calendar quarter fixed effects Jt in turnepend on national level policies as well as an unobserved random

rror �t with mean zero. To estimate the policy impact parameters2 in (5), we replaced the fixed effects Jt with their estimates Jt

rom the second stage Eq. (4). We then estimated the linear model

singleton female. For further details on maternal and pregnancy characteristics,ncluding descriptive statistics, see our working paper (Harris et al., 2014).

conomics 42 (2015) 186–196 193

(5) by OLS with Newey–West standard errors with a maximum lagof 4 calendar quarters to take account of possible heteroskedas-ticity and serial correlation of the error terms (Newey and West,1987). Similarly, we weighted the observations by the inverse ofthe standard errors of the estimates Jt .

Fig. 7 motivates the logic underlying the third stage of our anal-ysis. The vertical axis measures the estimated fixed effects Jt , whichrepresent calendar quarter-specific quit rates adjusted for individ-ual maternal characteristics, health center fixed effects, and thepresence or absence of a provider-level agreement. The horizon-tal axis measures the corresponding calendar quarter t. Highlightedare the dates on which the value added tax was imposed on tobacco,comprehensive tobacco legislation was passed, only brands with asingle presentation were permitted, images with warnings weremandated to cover 80% of the front and back of each pack, and thefifth and sixth rounds of images went into effect.

Columns (D) and (E) show the results of our three-stage proce-dure. Column (D) shows the estimate of �1 in Eq. (4) in the caseof FGLS with serially correlated errors. As in the previous models,the presence of provider-level agreement increased the probabilityof smoking cessation by 5.6 percentage points (p = 0.027). Column(E) shows the estimates of the policy impact parameters �2 in Eq.(5). The estimated policy impacts are comparable to those derivedfrom the 2-stage model (columns B and C). The point estimate ofthe impact of cigarette taxes is larger and statistically significant(p = 0.045), implying an estimated elasticity of quitting equal to0.36. Still, we could not reject the hypothesis that the estimated taximpact equalled that estimated from maternal-level data. Finally,the estimated effect of the five non-price policies combined wasindistinguishable from the estimates based on the individual-leveland two-stage models.

4. Impact on birth weight

We relied upon maternal-level data to assess the effect ofquitting smoking during pregnancy and birth weight. Following(Permutt and Hebel, 1989), we adopted a simultaneous equa-tion framework in which Uruguay’s anti-smoking policies servedas instruments for the endogenous variable of smoking cessa-tion. In addition, we took advantage of the birth-weight endpointto strengthen our identification of the causal effect of Uruguay’stobacco control campaign. Employing the population of non-smoking pregnant women as a control group, we performed afalsification test to determine whether the same policy instru-ments had any effect on the birth weight of infants delivered bynon-smokers.

We estimated the following equation on our sample of smokingpregnant women:

wist = ı1yist + c′iı0 + Ks + ςist (6)

where the variable wist denotes the birth weight of the infant deliv-ered by mother i in health center s and the calendar date t refers tothe midpoint of her third trimester of pregnancy. In Eq. (6), birthweight depends on smoking cessation (yist), individual maternalcharacteristics (ci), a health center fixed effect (Ks), as well as arandom error term (ςist) with zero mean.

If the random error ςist is correlated with yist, then the coeffi-cient ı1 will be biased when Eq. (6) is estimated by OLS. There is,in fact, good reason to believe that this is the case. For example, awoman with a propensity to engage in risky behaviors will tend not

to quit smoking and deliver a low-weight baby. In that case, failureto account for the unobserved heterogeneity will overestimate theparameter ı1. Alternatively, a woman who runs into complicationsduring her pregnancy will be under pressure to quit smoking and

194 J.E. Harris et al. / Journal of Health Economics 42 (2015) 186–196

0.1

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2007 2008 2009 2010 2011 2012 2013 2014

Calendar Quarter

80% Rule

5th RoundWarnings

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Value Added Tax Imposed on Cigarettes

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ig. 7. Trend in quit rate estimated from national-level model. The vertical axis meauit rates adjusted for individual maternal characteristics, health center fixed effectorresponding calendar quarter t. Highlighted are the dates on which various natio

end to deliver a low-weight baby. In that case, the parameter ı1ill be underestimated.

To address the potential endogeneity of the quit variable yist,e therefore estimated Eq. (6) by two-stage least squares (2SLS),here the first stage is defined by Eq. (1) and the instruments for

moking cessation are the policy variables xst and zt. As shown inable 2, estimation of Eq. (6) by OLS, with clustering of standardrrors by health center, gave an estimate of ı1 = 123.2 g (p < 0.001).y contrast, estimation of (6) by 2SLS, similarly with standardrrors clustered by health center, gave an estimate of ı1 = 187.9 gp = 0.028). While 2SLS increased the estimated standard error of

ˆ1, all tests rejected the hypotheses of weak instruments or over-dentification. Although the 95% confidence intervals of the twostimates of ı1 overlapped substantially, the results still suggesthat the OLS estimate may be biased downward.

For our falsification test, we used the parameters estimatedrom the first-stage Eq. (1) to predict the values of yist for thoseomen who did not report smoking during pregnancy. We then

stimated the model of Eq. (6) on all women in this comparisonroup, replacing yist with its predicted value. If the tobacco con-rol policies captured in the variables xst and zt in fact improvedirth weight by increasing the rate of quitting, then the estimatef ı1 in (6) should be indistinguishable from zero in the compari-on group of non-smoking pregnant women. On the other hand, ifhese policies are simply correlated with other unobserved factors

ˆ

hat improved birth weight, then the estimate of ı1 in (6) should beignificantly positive for non-smokers as well. In fact, as shown inable 2, the estimate of ı1 was indistinguishable from zero amongon-smokers (−27.8 g, p = 0.527).

able 2stimated effect of smoking cessation on birth weight.a,b

Population OLS 2SLS Falsification test

Smokers 123.2*** (10.8) 187.9** (85.5)Non-smokers −27.8 (43.8)No. observations 31,186 31,186 126,504

** Significant at p < 0.05.*** Significant at p < 0.01.

a All estimates correspond to the parameter ı1 in Eq. (6).b All standard errors adjusted for clustering by health center.

the fixed effects Jt estimated from Eq. (4), which represent calendar quarter-specific the presence or absence of a provider agreement. The horizontal axis measures thevel tobacco control measures went into effect.

5. Discussion and conclusions

To assess the impact of Uruguay’s nationwide tobacco controlcampaign, we analyzed a comprehensive nationwide registry ofpregnancies ending in a live birth during 2007–2013. We focusedsharply on smoking cessation among those women who reportedsmoking at any time during pregnancy, as well as the conse-quences of smoking cessation for birth weight. We observed astriking increase in the proportion of pregnant smokers who hadquit by their third trimester, from 15.4% in 2007 to 42.7% in2013.

We employed a difference-in-differences approach to evalu-ate the effects of provider-level agreements on quit rates duringpregnancy. We found that smoking cessation programs estab-lished under agreements between health centers and the NationalResource Fund increased quit rates by between 4.8 and 5.6 per-centage points. Unfortunately, no more than one-third of pregnantsmokers received care at health centers with contractual agree-ments during the period of analysis, and by 2013, the proportion ofwomen exposed to such treatments had declined. As a result, theseprovider-level agreements contributed little to the overall increasein smoking cessation observed during 2007–2013.

Although real taxes per pack increased by 122% during our studyperiod (Fig. 3), tax increases alone explained only about 20% of theoverall rise in smoking cessation during pregnancy. In addition,our estimates of the tax elasticity of quitting, ranging from 0.21 to0.36, were lower than those reported in the U.S. (Ringel and Evans,2001; Colman et al., 2003). The principal explanation for this limitedinfluence is that manufacturers moderated their retail prices inresponse to the application of the value added tax to cigarettesin July 2007 and other non-price regulatory policies enacted dur-ing 2007–2009 (Fig. 3) (Harris et al., 2014). As a result, the realretail price of cigarettes increased by only 17% during 2007–2013.Endogenous responses of the tobacco industry to state and nation-wide tax increases have been previously documented in the U.S.(Harris, 1987; Harris et al., 1996; Chaloupka et al., 2010; Miura,

2010).

To the contrary, most of the observed increase in quit rates wasattributable to non-price regulation of the marketing and packagingof cigarettes. While the combined effect of all five non-price policies

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as indistinguishable across the models that we tested (Table 1),t was nonetheless difficult to identify with precision the quanti-ative impacts of the individual component policies. We could notistinguish immediate versus long-run effects of policies, nor coulde identify synergies between policies. Our analysis at best identi-ed the average impacts of the tobacco control measures over time,onditional upon a specific temporal sequence of policy interven-ions. Thus, the increase in the size of warnings from 50 to 80% ofhe front and back of each pack of cigarettes, in effect since February8, 2010, was associated with a 3 percentage point increase in theessation rate (Table 1). However, this estimated impact was in theontext of the coincident fourth round of warnings, as well as aan on smoking in public places and private workspaces (March 1,006), the comprehensive tobacco control law (March 6, 2008), theingle presentation rule (February 14, 2009) and other policies inffect at the same time (Figs. 1 and 2).

While we had micro data on smoking cessation at the individualevel, the tobacco control policies that we evaluated were carriedut at either the health center level or the national level. Accord-ngly, if there were significant inter-correlation of quitting behaviormong women who attended the same health center or who wereregnant in the same calendar quarter, then the effective number ofbservations could be far less than the approximate 31,000 shownn column A of Table 1. However, our estimates on data aggregatedt the health center level (columns B and C) and at the national levelcolumns D and E) generally confirmed our individual-level results.

Some economists have suggested that the impact of smokingessation during pregnancy on birth weight, as estimated fromross-sectional databases, may be exaggerated by the presence ofnobserved heterogeneity (Lien and Evans, 2005; Abrevaya, 2006;brevaya and Dahl, 2008; Walker et al., 2009; Juarez and Merlo,013). That is, a woman who tends to engage in risky behaviorsill continue to smoke during pregnancy and have lower weight

abies. However, the presence of unobserved heterogeneity canlso result in an underestimate of the impact of smoking cessa-ion. Thus, a woman who encounters complications in the thirdrimester, such as intrauterine growth retardation, will quit smok-ng and have a lower weight baby. Our OLS estimate of the effectf quitting on birth weight was 123 g (95% CI, 102–145). When wesed Uruguay’s tobacco control policies as instruments for quit-ing smoking, our 2SLS estimate was 188 g (95% CI, 20–356). Whileur 2SLS estimate reinforces the conclusions that smoking cessa-ion during pregnancy, even in the third trimester, has a significantositive effect on birth weight, the confidence interval surroundinghat estimate was too wide to draw definitive conclusions about theirection of bias, if any, in the OLS estimate. Our results confirm thatven delayed cessation of smoking can reduce the adverse effectsf smoking during pregnancy (Lieberman et al., 1994; Raatikainent al., 2007; Batech et al., 2013; Yan and Groothuis, 2013).

As we have already noted, Uruguay’s tobacco control campaignas associated with declines in per capita cigarette consumption,

dult smoking prevalence and adolescent cigarette use that wereignificantly greater than those observed in Argentina, a countryith a common international border, language and culture that

erved as a control (Abascal et al., 2012). Unfortunately, we werenable to locate reliable nationwide data from Argentina on themoking practices of pregnant women during 2007–2013, and thusould not construct a comparable external control group for thistudy. Still, our falsification test took advantage of an internalontrol group, namely, pregnant Uruguayan women who did notmoke during pregnancy. We found, in particular, that the tobaccoontrol policies implemented in Uruguay during 2007–2013 had no

ffect on the birth weight of mothers in this non-smoking controlroup.

Our data on smoking from the SIP registry were self-reported. Its conceivable that Uruguay’s tobacco control campaign increased

conomics 42 (2015) 186–196 195

the social pressure on a pregnant woman to deny smoking whenqueried by her obstetrician. While we cannot completely rule outmisreporting bias, we note that if women had falsely reportedhaving quit smoking with increasing frequency as the campaignprogressed, we would have expected to see a growing reductionin the apparent favorable effect of quitting on birth weight. That isnot what we observed in Fig. 6. Moreover, if the apparent increasein smoking cessation during 2007–2013 were solely the result ofincreasing misreporting, then we would have observed no relationbetween quitting and birth weight. That is not what we observedin Table 2. In the context of smoking during pregnancy, a numberof authors have found a strong correlation between self-reportedcigarette consumption and objectively measured levels of nicotinemetabolites (Castellanos et al., 2000; Althabe et al., 2008; Himeset al., 2013).

During 2005–2009, the prevalence of smoking during pregnancydeclined from approximately 25% to 15% (Fig. 5). Unfortunately,missing data biases seriously complicated the interpretation ofprevalence trends thereafter. Moreover, there is evidence that somewomen who quit during pregnancy later resumed smoking andthen quit once again during the next pregnancy (Harris et al.,2014). Still, if the trend observed during 2005–2009 is an accurateindicator of an overall decline in prevalence, then our results onsmoking cessation may substantially understate the overall impactof Uruguay’s tobacco campaign.

Our results have important implications for future researchand for the future design of tobacco control policies. Our find-ings suggest that enhanced targeting of healthcare providers in theimplementation of tobacco cessation programs, as well as increasedrecruitment of patients, could have a high payoff. At the same time,our findings strongly suggest that non-price policies, in particu-lar regulation of marketing and packaging, can have an importantimpact in reducing tobacco use.

Financial support

We gratefully acknowledge the financial support of theBloomberg Foundation through an unrestricted grant to the Min-istry of Public Health (Ministerio de Salud Pública), Uruguay.Neither the Bloomberg Foundation nor the Ministry of Public Healthexerted any influence on the conduct of this study or the draftingof this manuscript.

Conflicts of interest

We have no conflicts of interest to declare.

Authors’ contributions

All three coauthors contributed to the conceptualization anddesign of this study, the analysis of the data, and the writing ofthis report.

Acknowledgments

We thank the Area Sistema Informático Perinatal from theEpidemiology Division of the Ministry of Public Health (UINS)for providing us with the perinatal data. We acknowledgevaluable inputs from Winston Abascal, Rafael Aguirre, Wanda

Cabella, Fernando Esponda, Elba Estévez, Marinés Figueroa, AnaLorenzo, Luis Mainero, Anna Mikusheva, and Giselle Tomasso.The opinions expressed in this paper are ours and oursalone.

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