The Intergenerational Impact of Terror: Did the 9/11 Tragedy Impact the Initial Human Capital of the Next Generation?


Given the unexpected nature of the terrorist attacks of September 11, 2001, a specific cohort of children were exogenously exposed to increased maternal psychological stress in utero. Rich administrative data and the precise timing of the event allow this study to uniquely provide insights into the health effects of exposure to maternal psychological stress across gestation. Results suggest that children exposed in utero were born significantly smaller and earlier than previous cohorts. The timing of the effect provides evidence that intrauterine growth is specifically restricted by first trimester exposure to stress; reductions in gestational age and increases in the likelihood of being born at low (<2,500 grams) or very low (<1,500 grams) birth weight are induced by increased maternal psychological stress mid-pregnancy. This study also documents a positively selected post-attack fertility response, which would bias an evaluation that includes cohorts conceived after September 11, 2001, in the control group.

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Data Availability

All data used for this article are publicly and freely available. The Vital Statistics Natality Birth Data is available at U.S. Bureau of Labor Statistics is available at


  1. 1.

    Eccleston (2011) provided evidence of this phenomenon for the specific case of NYC residents after 9/11. In Eccleston’s study, she showed that NYC and NY state income tax filings indicate that from 2001 to 2002, NYC experienced more, and higher income, emigration than the rest of NY state. In addition, she showed that the composition of exposed births in NYC had significantly more non-White mothers than previous cohorts.

  2. 2.

    For example, if exposure to an environmental stressor in the fourth month of pregnancy leads to an increase in births that occur at least one month early, using only date of birth to determine exposure timing will erroneously assign these poor birth outcome births to first trimester exposure and incorrectly suggest that first trimester exposure has a larger impact on birth outcomes.

  3. 3.

    One caveat to the advantage of using gestational age to assign exposure compared with birth month is that individuals conceived nine months prior to the event may not all remain in utero to experience exposure to the shock. Because the mechanism for the early timing of these births would be unrelated to the event, given that it has not occurred yet, the composition of these births will be mirrored by similar births in the control group and thus does not present an issue of endogenous selection. These births do, though, lead to measurement error for the cohort considered exposed in the last months of gestation because they are assigned to a treated group, but in truth are not exposed to the focal event. If this issue is present it would lead to estimates for the earliest conception month cohorts in the treatment group to be biased toward no effect. To assess the extent of this bias, all the main analyses in this article are also provided using the alternative method of assigning exposure based on birth month. These results, presented in the tables of section B in the online appendix, provide no evidence that the use of gestational age to assign exposure is leading to substantial underestimation or incorrect inference regarding the impact of late gestation exposure to maternal psychological distress on birth outcomes.

  4. 4.

    Researchers have argued that some elements of the birth certificate data, especially parental characteristics and gestational age, are incomplete and imprecise (Reichman and Hade 2001). In terms of measurement error resulting from imprecise gestational age information, because there is no reason to think the inaccuracy would have a specific pattern or relationship to the timing of 9/11, the only concern would be less precision in the estimated coefficients. The power gains from the large sample size do to an extent, though, help to offset this concern. With regard to missing information, the primary dependent variable—birth weight—is missing for only .1% of the sample, and there is no evidence that lack of birth weight information is related to 9/11 exposure. In addition, only 2.8% of the sample is missing any information used in the primary specification. In the main analysis, when a control variable has missing information, it is assigned the mean value from the sample and for each variable an indicator that identifies observations with missing information is added to the regression. Results are comparable when alternatively any individual with a missing value for an independent variable is dropped.

  5. 5.

    Robustness checks that additionally exclude individuals from the entire New York City metropolitan area are also conducted and included in section A of the online appendix.

  6. 6.

    One potential concern is that because gestational age is predominately calculated based on women’s self-reports, if error in this measure is systematically related to 9/11 it could bias the results. The most plausible way this type of nonrandom misreporting could occur is if pregnant women were less likely to obtain or delayed prenatal care following the terrorist attack, given that knowledge and accuracy of gestational age is partly based on health care usage. As discussed in the section Parental Composition and Maternal Behaviors, this is not the case.

  7. 7.

    Birth month is the finest level of birth date information available for each child.

  8. 8.

    For example, for a gestational age of 36 weeks and birth month of 12, the conception week would be calculated in the following way. The gestational age minus 2 and divided by 4 is 8.5, suggesting that conception occurred 8.5 months before birth. Subtracting 8.5 from the birth month, 12, suggests the estimated conception week was the third week of March. Alternatively, for a birth month of 3, subtracting 8.5 from the birth month would give –5.5. Because this value is less than 1, 12 would be added back to give 6.5, or the third week of the previous June.

  9. 9.

    In the previous example in which gestational age was 36 weeks and the birth month was 12, conception year would equal birth year. Alternatively, in the example in which the birth month was instead 3, conception year would equal birth year minus 1.

  10. 10.

    As I discuss in the upcoming main analysis section, cohorts conceived after the event are from endogenously and positively selected families, and thus their inclusion would jeopardize the randomness of the treatment/control designation.

  11. 11.

    In section B of the online appendix, the results are checked for robustness to additionally including controls for county-level economic conditions.

  12. 12.

    When a characteristic of the mother has a missing value, it is replaced with the mean value from the sample, and an indicator variable is created and included for each characteristic that equals 1 if the information for that factor is missing. Results do not qualitatively or quantitatively differ if all observations missing a value for any independent variable are instead dropped. Results available upon request.

  13. 13.

    Given the nonstandard form that must be used for the cohort fixed effects, alternative controls for temporal heterogeneity have also been assessed. In Table A1 of the online appendix, the six 16-month interval fixed effects are replaced by linear splines using 6 periods, linear splines using 10 periods, quadratic trends, or 10-month fixed effects. In each case, the magnitudes of the coefficients are qualitatively and quantitatively equivalent, or larger, and the pattern is similar.

  14. 14.

    Alternatively, an approach that estimates conception date as nine months prior to birth date—mirroring what is typically found in the literature when using only birth timing information—is provided in Table B1 of the online appendix. This approach uses all infants delivered before June 1, 2002, in an effort to limit the sample as much as possible, to children conceived prior to the event. Similarly, for births in September 2001, it cannot be determined whether they were exposed or not. Thus, as an attempt to err on the side of a nonresult, I considered them to be part of the control. Specifically, I estimate the following equation:

    $$ {b}_{im jt}={\upalpha}_0+{\mathbf{Treat}}_i^{\prime}\upbeta +{\mathbf{X}}_{im}^{\prime}\updelta +{\upgamma}_{yrproxy}+{\upgamma}_{month}+{\upgamma}_j+{\upgamma}_{yrproxy,j}+{\upvarepsilon}_{im jt}, $$

    In this equation, the matrix Treat is eight indicators of being born in one of the eight months from October 2001 to May 2002, representing the exposure period. Although true birth year fixed effects are not included, six 16-month interval fixed effects, γyrproxy, will serve as controls for time trends, and seasonality is controlled by birth fixed effects, γmonth. To account for unobserved heterogeneity that is time-invariant within the mother’s residence state, I add dummy variables for mother’s state of residence to the model, γj. Finally, the interaction of an observation’s 16-month birth interval and mother’s state of residence, γyrproxy,j, are incorporated into the specification.

  15. 15.

    Birth weight–for–gestational age z score is calculated as an infant’s birth weight minus the mean birth weight from 1995 to 2000 for that infant’s gestational age, all divided by the standard deviation of birth weight from 1995 to 2000 for that infant’s gestational age.

  16. 16.

    Maternal characteristic controls are excluded from these regressions.

  17. 17.

    Equivalent summary statistics are provided by conception year in Tables C1C7 in the online appendix.

  18. 18.

    Table 1 indicates that at times, maternal information is missing in the birth records. In terms of control variables, the issue of missing information is minimal. Specifically, live birth order is missing for 0.5% of records, gestational diabetes status is missing for 1.2% of records, and mother’s years of education is missing for 1.3% of records. When a characteristic of the mother has a missing value, it is replaced with the mean, and an indicator variable is created and included for each characteristic that equals 1 if the information for that factor is missing. Results do not qualitatively or quantitatively differ if all observations missing a value for any independent variable are instead dropped. Missing values for maternal pregnancy behaviors are more prevalent: 1.9% of records are missing prenatal care information, 20.1% of records are missing maternal weight gain information, 17.7% of records are missing gestational smoking behavior, and 14.8% of records are missing gestational alcohol use. With regard to the impact of potential measurement error or sample selection bias in these variables, because there is no reason to think the missingness or inaccuracy in these variables would have a specific pattern or relationship to the timing of 9/11, the only concern would be loss of external validity and less precision in the estimated coefficients for regressions that use those behaviors as the dependent variable.

  19. 19.

    The risk factor estimates are calculated as the increased incidence divided by the mean incidence in the population.

  20. 20.

    I also conduct similar alternative specifications using only birth data information. The results from these regressions mirror those presented in this section, providing evidence of the robustness of Table 2’s findings. These estimates are shown in Tables B2B5 in the online appendix.

  21. 21.

    The economic activity from approximately six months after birth is included in case the parents are able to reasonably predict coming economic hardship/prosperity and made earlier adjustments to their consumption that would affect the relevant pregnancy.

  22. 22.

    Maternal characteristic controls are excluded from these regressions.

  23. 23.

    As shown in Table 1, there are a nontrivial number of observations missing alcohol (14.8%) and smoking (17.7%) behavior. In addition, these variables have strong potential for being measured with error. However, because it is unlikely that the missingness or possible inaccuracy is caused by or related to the 9/11 attacks, these issues, at worst, lead to a decrease in external validity and precision, but they do not generate bias.

  24. 24.

    Similarly, there is no evidence of gender heterogeneity in the impact of maternal psychological stress in utero on gestational age. Results are available upon request.


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Financial support was provided by a T32 Training Grant in the Social, Medical, and Economic Demography of Aging from the National Institute on Aging/National Institutes of Health. I am very grateful to Duncan Thomas, Seth Sanders, Erica Field, Elizabeth Frankenberg, V. Joseph Hotz, Alessandro Tarozzi, and Andrea Velasquez for their comments while developing this article.

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Brown, R. The Intergenerational Impact of Terror: Did the 9/11 Tragedy Impact the Initial Human Capital of the Next Generation?. Demography (2020).

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  • Birth weight
  • Maternal health
  • Fetal health
  • Psychological distress