Methodological challenges when estimating the effects of season and seasonal exposures on birth outcomes

Worldwide, it is estimated that 2.2% of all babies are stillborn [1] and 9.6% of all births are preterm (less than 37 completed weeks of gestation) [2]. Preterm babies are at greater risk of poor health and early death, require longer periods of hospitalisation after birth, and are more likely to develop disabilities [3‐5].

Environmental and meteorological factors may be a cause of adverse birth outcomes [6]. Increases in air pollution [7] and temperature [8] have been associated with adverse birth outcomes. Air pollution and temperature usually have a strong seasonal pattern, meaning that one method of examining environmental factors is to explore seasonal patterns. Research has shown that the risk of preterm birth varies by season of birth [9, 10] and season of conception [11]. Seasonal patterns of preterm birth differ from country to country, and peaks have been shown to occur at both hot and cold times of the year. For example, in a London cohort of almost 500,000 live singleton births, babies were more likely to be born preterm in winter than in spring (odds ratio = 1.10, 95% confidence interval (CI) 1.07-1.14), with the highest risk of preterm birth in November and December (probability of 0.76 per 1,000 fetuses at risk compared to 0.64 in April) [12]. However, in Greece preterm birth rates were highest in summer and spring [9], and in The Gambia preterm birth rates peaked in summer and autumn [13]. In Japan peaks of preterm births were reported in summer and winter [14]. The peak in winter was dominant among the northern latitudes and the peak in summer was dominant among the southern latitudes, suggesting that the seasonal pattern was dependent on factors differing between geographic locations (such as temperature) [15]. Different statistical methods may partly explain the differences in the seasonal patterns in the studies discussed above [16]. In particular, some studies assumed a sinusoidal seasonal exposure, whereas others looked at individual months or seasons.

Studies in developing countries have hypothesised that seasonal patterns in birth outcomes are due to seasonal changes in nutrition, infectious diseases, and seasonal work [13]. These factors are not as important in developed countries, but seasonal patterns in birth outcomes still occur, possibly because of seasonal changes in Vitamin D, air pollution or temperature [7, 8, 17, 18]. As we show in this paper, seasonal patterns can also be due to biases in the selection of the study sample.

Table 1 describes the demographics of the original Brisbane cohort (n = 114,947). Figure 2 shows gestation lengths by month and year of conception. The births in the cohort conceived in September 2004 must have had a gestation of at least 40 weeks to be included, because any shorter pregnancies gave birth before the start of the study period (1 July 2005). The closer to the start of the study period, the more possible it became for women with shorter pregnancies to enter the cohort. In the middle of the cohort, gestation lengths were relatively stable, as all pregnancies were included and none were excluded because of their length. Towards the end of the cohort it became impossible for women conceiving during the study period but with longer pregnancies to be included, because they gave birth after the end of the study period. After removing the pregnancies conceived more than 19 weeks before the study start and less than 43 weeks before the study end, the adjusted cohort had 101,870 pregnancies (88.6% of the original sample).

Artificial seasonal patterns can occur in retrospective birth cohorts depending on the study's start and end dates (Figure 3). The cause is the great difference in pregnancy lengths between those births included at the start and those included at the end of the study. In our Brisbane cohort the median gestation length was 40 weeks at the start of the study, 39 weeks in the middle part of the study and as low as 25.5 weeks during the last conception month (Figure 2). The artificial seasonal patterns caused by the fixed cohort bias have a shape similar to an expected seasonal pattern, meaning that it could easily be wrongly attributed to a seasonal exposure (e.g., temperature). It is possible to remove the bias at the cost of a loss of sample size. We demonstrated how the bias was avoided by removing the pregnancies that were conceived earlier than 19 weeks prior to the start of the study period and later than 43 weeks before the end of the study period (Figure 4).

The biases are not caused by the well-known issues of censoring in survival data, which occurs when the start or end time of a subject are unknown. The bias demonstrated here is because both the start and end times are unknown. It is a bias caused by subjects who were completely (and unknowingly) missed from the cohort, not because of subjects who were partially observed.

The potential biases due to changes in the at-risk population when examining the effect of time-dependent exposures on pregnancy have been addressed by two recent studies [19, 22]. These studies showed substantial biases due to ignoring seasonal patterns in pregnancies [19], and due to ignoring the week of gestation at study entry [22]. A recent study demonstrated the value of using time-dependent exposures as part of a Cox proportional hazards model when estimating the effects of air pollution on pregnancy, and concluded that this method was more effective than conventional approaches for estimating key exposure periods [23]. We also recommend the use of methods that adjust for the at-risk population and use time-dependent exposures to correctly estimate the effects of environmental exposures on pregnancy. However, we caution that when using these methods the fixed cohort bias needs to be considered. Our paper makes an important contribution to this developing area as it shows the potential size of the fixed cohort bias and a simple way to avoid it.

Our results show how the size of the fixed cohort bias can be substantial, causing great changes in the months that most effect gestation length (Figure 3, 4), and changing the estimated effect of temperature on gestation length (Figure 5). The results in Figure 3 showing the erroneous seasonal pattern were based on four years of data. To remove the seasonal pattern we excluded pregnancies with conception dates 19 weeks before the cohort started and 43 weeks before the cohort ended. These were around 13% of all pregnancies, and so represent a relatively large proportion of the sample, which explains the relatively large bias.

As shown in Figure 3, the fixed cohort bias is avoided when the day and month of the cohort's end date are a day before the day and month of the cohort's start date (regardless of year). A design with these 'matching' start and end dates is the most common for previous birth cohort studies [11, 18, 24, 25]. However, the balancing of the bias will not occur for time-dependent exposures. For example, if there was an unusually hot month in the first trimester of those women captured at the start of the study, then high temperatures could be wrongly associated with longer gestations. The bias would only be avoided if there was an equally unusually hot month at end of the study period, when the women captured in the cohort have shorter gestations. We examined this potential bias in the original and adjusted Brisbane cohort and confirmed that the fixed cohort bias changed the effect estimates of temperature on gestation length (Figure 5). Ignoring the fixed cohort bias meant the biggest changes in the hazard ratios were at the extremes of temperature, whereas the adjusted estimate shows the biggest changes for more moderate temperatures. So if we ignored the fixed cohort bias we might wrongly advise that pregnant women avoid extreme temperatures (above 25°C), whereas the actual change in gestation length is for moderate temperatures (between 16 and 25°C). The fixed cohort bias can therefore not only bias the estimated effects of season (e.g., month of conception), but can also bias the estimated effects of seasonal exposures (e.g., air pollution and temperature).

A group of conceptions that were missed in this study were those occurring before 20 weeks (spontaneous abortions). These unfortunate cases are not added to the Brisbane birth registry. Rates of spontaneous abortions having reached at least five gestational weeks after last menstrual period vary from 11 to 16% [26‐28]. Missing these cases has the potential to bias estimates of time-dependent exposures. Suppose an environmental exposure is strongly associated with spontaneous abortion, then a peak in this environmental exposure will cause an increase in spontaneous abortions and hence a decrease in the number of births that appear in the cohort. A study based on births after 19 weeks would miss the opportunity to detect the dangers of this exposure. Hence birth cohort studies should minimise their entry time, and clarify that the results only apply to pregnancies that have progressed to that time.

An ideal study design is one that prospectively follows women from close to conception, as this ensures that no pregnancies are missed (and hence the fixed cohort bias is not an issue). However, these designs are much more expensive that those relying on routinely collected birth data. A good alternative is to adjust cohorts using our method, and so avoid artificially created patterns and wrongly estimated effects from seasonal environmental exposures on birth outcomes.

Our results in Figure 5 are consistent with three previous studies that found that exposure to high temperatures in the week of birth increased the risk of preterm birth [8, 9, 29]. Maternal hyperthermia has been associated with abortions and stillbirths with lags of days to several weeks [30]. A study investigating hot tub and Jacuzzi use during the pregnancy and its effect on abortions found that pregnant women using hot tub or Jacuzzi during the pregnancy were twice as likely to have an abortion than women who did not (hazard ratio: 2.0, 95% confidence interval: 1.3, 3.1). Another study found that application of heat to the abdominal wall of women in labour increased uterine activity [31]. Dehydration during warmer temperatures may also be the cause of the shorter gestations, as insufficient fluids in the mother can decrease the amount of blood available to the fetus and induce uterine contractions [32]. Our results suggest that pregnant women should avoid exposure to high temperatures.

Correctly estimating the effects of environmental exposures on pregnancy is vital because an unhealthy start to life can mean an unhealthy adulthood. The adverse health effects of preterm birth and low birth weight include: socio-emotional and educational problems [3], reduced cognitive function [4], impaired vision and hearing [5] and restricted growth [34]. New research into the possible effects of the temperature on pregnancy is particularly important because of climate change. Future changes are predicted to include an increase in 'mega-heatwaves' such as those experienced in Europe in 2003 and 2010 [35]. If higher temperatures increase the risk of preterm birth as shown here (Figure 5), then we can expect a greater future public health burden due to preterm birth.