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For decades, epidemiologists have observed that, among lower birth weight infants, higher risk infants have lower mortality rates than do lower risk infants. However, among higher birth weight infants, the pattern reverses, leading to a riddle of crossing birth weight-specific mortality curves. The riddle has been considered from different perspectives, including relative z scores, directed acyclic graphs, and, most recently, simulated mathematical models of underlying causal factors that produce the observed curves; similarly paradoxical gestational age-specific mortality curves uncross when calculations include all fetuses-at-risk rather than just infants delivered at a particular gestational age. However, researchers have generally focused on birth weight rather than gestational age, likely because birth weight is accurately measured and, if one assumes that birth weight is an intermediate variable between the underlying causal factors and mortality, is easier to model. Within the framework of existing analytical approaches, adding the complexity of a direct relation between gestational age and mortality, and possibly more complex relations among the casual factors, may be difficult. Nevertheless, duration of pregnancy seems a better proxy for the true construct of interest, whether the baby is mature enough to survive, so shifting attention to understanding the riddle of gestational age-specific mortality is encouraged.
For decades, epidemiologists have observed that, among lower birth weight infants, higher risk infants have lower mortality rates than do lower risk infants. However, among higher birth weight infants, the pattern reverses, leading to crossing birth weight-specific mortality curves (1–3). The paradox of better survival of lower birth weight infants for traditionally higher risk compared with lower risk groups (e.g., defined by smoking (1, 2) and race (3)) has complicated clinical decisions for low birth weight infants. Although uncrossing these curves is not the final goal (4), attention to this paradox has provided a stepping stone for perinatal epidemiologists toward understanding factors related to infant mortality.
The paper by Basso and Wilcox (5) in this issue of the Journal builds on their previous work (6) that demonstrated that the influence of 2 unknown, rare, and potent confounding factors, X1 and X2, could shift the target birth weight distribution, increase the risk of mortality, and produce observed birth weight-specific mortality curves, even assuming no direct effect of birth weight on infant death. In their current paper, Basso and Wilcox widen this framework to show how X1 and X2 could produce observed crossing birth weight-specific mortality curves for groups with differing birth weight distributions and underlying risks of mortality. Within a particular stratum of observed birth weight, the distributions of X1 and X2 differ between groups, leading to different mortality risks— hence, the observed crossover.
In this paper, we illustrate some approaches that have hypothesized reasons for crossing birth weight-specific mortality curves (7–11). With some exceptions (3, 12–15), less attention has been directed toward similarly paradoxical gestational age-specific mortality curves. Although stretching the ideas of Basso and Wilcox (5) and Basso et al. (6) to gestational age-specific mortality does not directly follow from their methodology, we argue below that the results would be worth the extra effort.
Over 20 years ago, Wilcox and Russell hypothesized that birth weight-specific infant mortality curves between groups should be compared relative to each group's so-called target birth weight distribution rather than to their observed birth weight; comparisons of birth weight-specific mortality by race (7), smoking status (8), and parity (9) uncrossed when group-specific birth weight z scores were compared rather than observed birth weight. Hertz-Picciotto and Din-Dzietham (12) applied this idea to percentiles of gestational age with similar results.
Another theory is that paradoxical crossovers result from the wrong statistics being calculated (13–15). Specifically, these investigators propose that the proper denominator for perinatal mortality calculations should be fetuses-at-risk, not just infants born during a specific gestational week. When the gestational age-specific risk of mortality is defined by using all fetuses who survived to that gestational age or later in the denominator, rather than births at that gestational age, perinatal mortality curves for high and low risk groups uncross. (Although these studies focus on gestational age-specific mortality, the essential idea can be applied to birth weight-specific mortality by using the number of births at a particular weight or heavier in the denominator.) Using this method to examine mortality beyond the neonatal period, Platt et al. (14) applied an extended Cox regression model, where all fetuses and infants alive at a certain post-last menstrual period week were at risk, and uncrossed mortality curves defined by race and smoking status. In the analysis of Platt et al. of fetuses/infants-at-risk, an infant born at 34 weeks' gestation who survived 2 weeks and an infant who was born and died at 36 weeks' gestation were both considered deaths at 36 weeks post-last menstrual period; gestational age at birth was included in the survival model as a covariate.
Other recent approaches to analyzing these relations have not sought to uncross the curves. Rather, by thinking beyond the available data, proponents of these approaches hypothesize unknown factors that cause mortality and, in doing so, generate the empirical relations. Basso and Wilcox, for example, characterize the unknown factors, X1 and X2, by their prevalence and their potencies using hypothetical and empirical definitions of F (high and low risk groups), albeit using simple models with strong underlying assumptions. What is gained from this approach is not a complete picture of these unknown factors, as more details are needed to fully understand these issues; however, Basso and Wilcox have postulated a way to augment available data to add insights into observed relations and to characterize unknown causes.
Separately, Hernández-Díaz et al. (10, 11) used directed acyclic graphs (DAGs) to show that selection bias arising from stratification on a common effect, in this case stratification by birth weight, could lead to misleading results. Like Basso and Wilcox (5) and Basso et al. (6), Hernández-Díaz et al. include an undefined risk factor in their graphical model. Briefly, following the notation of Basso and Wilcox (5) and Basso et al. (6) and focusing on X1, consider stratified intervals of birth weight and 2 variables, F and an unknown factor, X1, which are both related to birth weight and the risk of mortality but not to each other. DAGs show how the stratified relation between F and mortality can be distorted by the induced association between F and X1 within 1 or more strata. As mentioned by Basso and Wilcox (5), DAGs can show how z-score comparisons eliminate selection bias by removing the arrow between F and birth weight.
Let us accept the assumption of Basso and Wilcox (5) and Basso et al. (6) that birth weight per se has no direct effect on mortality and that, at least cross-sectionally, mortality is lowest among term infants. If true, then why do investigators continue to study birth weight, and why do they study it among term births? The probable if unspoken answer is that birth weight is accurately measured (16), and gestational age is usually correct when it indicates a term birth (17). Furthermore, term birth weight is approximately normally distributed and unhindered by the exclusion of fetuses still in utero (18). Put simply, we are looking where looking is easy. Measuring the duration of pregnancy is inherently more error prone than measuring size at birth; gestational duration in the large administrative database of vital records has substantial inaccuracy, especially at low values. Nevertheless, although birth weight may be easier to model and has served to “lay the ground rules” for approaching the problem, gestational duration seems to us a better proxy for the true construct of interest—whether a baby has attained sufficient maturity to survive outside the uterus.
However, if we apply the approach of Basso and Wilcox (5) to investigate gestational age-specific mortality as the outcome of interest rather than gestational age as a risk factor F, the implications of their framework quickly become more complicated. As Schisterman and Hernández-Díaz (19) show in their 2006 editorial on the original work of Basso et al., if birth weight has some effect on mortality, then a large number of scenarios exist. When extending the framework to gestational age, we believe one must allow for the assumption of the direct effect on mortality cautioned by Schisterman and Hernández-Díaz. Consider mistimed voluntary cesarean delivery, mistimed voluntary termination of pregnancy, or maternal illness unrelated to pregnancy that requires the pregnancy to be delivered early (such as the need for chemotherapy when cancer is diagnosed during pregnancy). We believe that, in these situations, neither the underlying reason for the elective procedure nor the factors resulting in mistiming are direct causes of mortality. Yet infants born in these situations can suffer all the usual consequences of early birth (20). Given that the duration of pregnancy per se could be a direct cause of mortality, extensions of existing models need to include a structure for this underlying relation.
We suppose an extension of the framework of Basso and Wilcox to allow for effects of X1 and/or X2 on mortality to depend on gestational age. Consider 2 scenarios based on X1, an unknown factor that reduces gestational age and is associated with mortality. The first is a situation where the intrauterine environment created by X1 could be more harmful than the risks associated with preterm birth; that is, among pregnancies affected by X1, the mortality risk would be higher for term compared with preterm infants. For example, it has been postulated that the fetus responds to infection by triggering labor, and failure of the fetus to do so is observed as a stillbirth (21). The second scenario is a situation where X1 could directly harm the fetus while in utero and simultaneously make it less able to survive when born at early gestational ages. Folic acid deficiency, for example, could lead to preterm birth (22) and increase the risk of mortality through an increased risk of congenital anomalies (23). Further, if infants with congenital anomalies have a poorer prognosis at earlier compared with later gestational ages because of treatment options or success rates, this deficiency could lead to an additional risk of mortality for infants with both outcomes, greater than the combined risk (on some scale) of preterm birth and congenital anomalies.
If we evaluated these 2 scenarios, we would observe that births affected by X1 shifted to earlier gestational ages and corresponding increases in deaths at those gestational ages caused by preterm birth. However, the change in the total number of deaths would be modified by the cause of preterm birth. Under the first scenario, where the preterm birth is less dangerous to the fetus than remaining in utero, increased risks of death for low gestational ages would be coupled with changes in risks at later gestational ages. Under the second scenario, where the mortality risk from preterm birth is further increased for compromised infants, more deaths would occur at the realized gestational age. With the assumption of a relation between gestational age and mortality, an approach along the lines of Basso and Wilcox (5) and Basso et al. (6) could likely reproduce the empirical gestational age-specific mortality curves explained in part by different proportions of X1 within each week of gestational age, although solutions may not be unique. By use of a fetuses-at-risk approach, the shift in the gestational age distributions caused by X1 leads to fewer fetuses at risk in the denominators at later gestational ages and larger numbers of deaths at earlier ages, much like the effects of F, where higher risk groups have more births and deaths at earlier gestational ages.
Under our assumption that the duration of pregnancy can have a direct effect on mortality, the magnitude and direction of which depend on the underlying cause of delivery, modeling these relations may need to be based on fetuses/infants-at-risk approaches (14), albeit with more investigation of the role of birth in the models (24). Such modeling requires that causes of delivery can be measured, which sadly at this time is little more than a pious hope. Although the fetuses/infants-at-risk approach has the advantage of being based on cohort theory, its proponents have not, to our knowledge, taken it beyond cohort theory to contrast scenarios implied by fetuses/infants at risk to those implied by conventional analysis.
When DAGs for these scenarios are developed, different causes of early delivery might result in qualitatively different directed edges from gestational age to death. Although conventional DAGs are indifferent to the strength and direction of associations, characteristics of the groups, and traits of the unknown factors, their structure allows for the exploration of alternate scenarios. However, mathematical models that explore the results predicted by DAGs must account for both magnitude and direction. Recent contributions by VanderWeele et al. (25) that extend these graphs to include the direction of effect, as well as contributions by VanderWeele and Robins (26) that extend these graphs to include effect modification, may be able to better represent these scenarios.
In summary, our first recommendation is for investigators to carry these lines of investigation to the association between duration of pregnancy and mortality, complexity and all. Second, we recommend that fetuses/infants-at-risk approaches be considered for modeling these complex relations; however, particular attention to both the role of birth in the models and examinations of comparable relations implied by more traditional analyses is needed. Although we can line up putative causes of preterm birth and investigate how they fit into these and other causal model frameworks, the challenge will be to maintain the delicate tension between Basso and Wilcox's elegant simplicity that allows for an “ah-ha moment” and the added complexity needed to evaluate plausible scenarios. Otherwise we may find ourselves back where we began, looking where looking is easy.
Author affiliations: Office of Analysis and Epidemiology, National Center for Health Statistics, Centers for Disease Control and Prevention, Department of Health and Human Services, Hyattsville, Maryland (Jennifer D. Parker); and Division of Epidemiology, Statistics, and Prevention Research, Eunice Kennedy Shriver National Institute of Child Health and Human Development, National Institutes of Health, Department of Health and Human Services, Bethesda, Maryland (Mark A. Klebanoff).
Dr. Klebanoff was supported by Intramural Program funds from the National Institute of Child Health and Human Development, National Institutes of Health.
The findings and conclusions in this paper are those of the authors and do not necessarily represent the views of the National Center for Health Statistics, Centers for Disease Control and Prevention.
Conflict of interest: none declared.