Editorial In Bed with The Devil: Recognizing Human Teratogenic Exposures

As teratologists, we seek to prevent children from being harmed by exposures that their mothers have during pregnancy. We cannot do this without knowing that such effects exist, and this puts us in bed with the Devil: The only way we can ever know with certainty that an exposure is teratogenic in humans is to recognize that it has caused birth defects in children. Our challenge is to do this as quickly and efficiently as possible, when the fewest babies have been harmed. Proving that an association observed between an exposure and an adverse outcome in humans is causal is usually done by assessing the available evidence according to a set of “considerations” laid out by Sir Austin Bradford Hill more than 50 years ago (Table 1) (Hill, 1965). Although critics abhor the misuse of these criteria as a diagnostic algorithm (Phillips and Goodman, 2004; Ioannidis, 2016) or argue that they inappropriately emphasize epidemiological evidence over mechanistic understanding (Howick et al., 2009; Fedak et al., 2015), the Bradford Hill criteria continue to be widely used as a framework for thinking about causal inferences in medicine, but not in teratology. The Bradford Hill criteria are rarely, if ever, used in human teratology research because they assume the availability of multiple high-quality epidemiology studies, and most pregnancy exposures have not been adequately assessed by such studies (Lo and Friedman, 2002; Adam et al., 2011). This is not surprising: Well-powered epidemiology studies of teratogenic birth defects usually require many hundreds or thousands of babies to be born with birth defects before causality can be established. A second major limitation of using the Bradford Hill framework for teratology studies is that it does not take into account recurrent distinctive patterns of congenital anomalies like the fetal alcohol syndrome, thalidomide embryopathy, or congenital Zika syndrome, that have permitted the recognition of most human teratogenic exposures (Jones and Carey, 2011). Recognizing that an exposure is teratogenic in humans requires three things: (1) the occurrence of babies with birth defects caused by the exposure, (2) a way to associate the pregnancy exposure with the birth defects (hypothesis generation), and (3) a way to prove that the observed association is causal (hypothesis testing). My focus here is on the third point. Complementary evidence of several different kinds is necessary to infer that a particular maternal exposure during pregnancy causes birth defects in humans. This evidence may include experimental studies in model systems, case reports and clinical series, and epidemiology studies. Experimental studies in model systems provide the opportunity to identify exposures that have teratogenic potential without harming any children. Prescription medications are routinely tested before marketing for their teratogenic potential using standard protocols in rats and rabbits (Wise et al., 2009). Many other agents undergo mammalian teratology testing because they are widely used or have properties that raise concern about possible developmental toxicity (Buschmann, 2006; Beekhuijzen, 2017). A variety of nonmammalian in vivo, in vitro, or in silico tests have also been developed to provide more cost-effective or humane alternatives for identifying the teratogenic potential of exposures (Augustine-Rauch et al., 2011; Robinson and Piersma, 2013; Scott et al., 2013; He et al., 2014; DeSesso, 2017). Unfortunately, the findings in experimental systems sometimes differ from those observed in humans (Brent, 2004; Daston, 2011). This is expected because model systems all differ from human pregnancy to some extent with respect to pharmacology, physiology, biochemistry, anatomy, placentation, and embryonic development. In addition, experimental models are designed to be uniform and reproducible, while pregnant women differ from each other with respect to underlying illnesses, concomitant exposures, and genetic factors. Experimental studies are essential for elucidating the mechanisms that underlie teratogenic effects, but such studies are neither necessary nor sufficient to prove that an exposure is teratogenic in humans. Case reports are clinical descriptions of children with congenital anomalies or other adverse outcomes whose mothers experienced a particular exposure during pregnancy. Clinical series are collections of such anecdotal reports. Case reports and clinical series are useful for raising causal hypotheses about human teratogenic effects. Observations by alert clinicians of an extremely rare pattern of congenital anomalies among children born to women who had the same unusual exposure during pregnancy are the most sensitive means of surveillance we have for human teratogenic effects. Rubella embryopathy (Gregg, 1941; Lande, 1950), thalidomide embryopathy (Lenz and Knapp, 1962; Speirs, 1962), fetal alcohol syndrome (Jones et al., 1973; Clarren and Smith, 1978), congenital Zika syndrome (de Fatima Vasco Aragao et al., 2016; Schuler-Faccini et al., 2016; Moore et al., 2017), and many other major human teratogenic effects were first suspected by alert clinicians who observed affected cases and raised an alarm (Jones and Carey, 2011). Recognition of teratogenic effects through case reports and clinical series is highly sensitive but has poor specificity. Most anecdotal observations of the occurrence of an exposure in a woman's pregnancy and birth defects in her baby are coincidental, not causal. Congenital anomalies are diagnosed in 2 to 3% of infants (Kucik et al., 2012; Feldkamp et al., 2017), and developmental disabilities are even more frequent (Van Naarden Braun et al., 2015; Zablotsky et al., 2015). Maternal exposures to medication occur in at least half of all pregnancies (Palmsten et al., 2015; Smolina et al., 2015), and other exposures during pregnancy are also common. Given the frequency both of exposures and of birth defects, it is not surprising that they often occur together by chance. Even if a particular pregnancy exposure actually causes the birth defects observed in an infant, this association cannot be quantitated, tested statistically, or proven by case reports or clinical series alone. Recognition of a distinctive pattern of congenital anomalies in association with a teratogenic exposure is only possible if the same pattern of anomalies recurs repeatedly in children born to women who had similar exposures during pregnancy and is extremely rare (or nonexistent) in children born of unexposed pregnancies. Causal inference is strengthened if the specific exposure is also rare and can unequivocally be established to have occurred in the pregnancies of women who subsequently gave birth to affected infants. Epidemiology studies are the only reliable way to obtain quantitative estimates of risk and statistical significance associated with human teratogenic exposures. Randomized controlled trials are the optimal design for hypothesis testing but are rarely used in birth defects epidemiology. It would be unethical to conduct a randomized controlled trial to determine if a particular maternal exposure caused congenital anomalies in the infants. Treatment trials in women with chronic or pregnancy-related illnesses can be assessed for teratogenic risks, but information on the health status of the infants is rarely collected in a rigorous manner in such studies. Cohort studies are observational comparisons of the frequency of congenital anomalies or other adverse outcomes among the children of women who had a particular exposure during pregnancy and the children of women who did not have that exposure. Cohort studies are especially valuable because they directly address the questions that most pregnant women and their health-care providers have about teratogenic risks: Does this exposure increase the risk of birth defects in the baby, and, if so, by how much? Some cohort studies collect information on exposures and outcomes of all pregnancies in a population. Because most specific exposures (e.g., treatments with one specific drug) and most birth defect outcomes are infrequent, population-based cohort studies must include hundreds of thousands or millions of births to have sufficient statistical power to be informative for most exposures. Such studies are expensive, and not many are done. Cohort studies can also be done by collecting information on the outcomes of pregnancies of women who had a particular exposure and pregnancy outcomes of appropriate control women. Exposure cohorts of this kind can be assembled through teratogen information services, which women contact for counseling regarding the risks of these exposures during pregnancy, or through drug- or disease-specific pregnancy registries that collect data on both exposed and comparison pregnancies. Because they focus on the pregnancies of women with particular exposures of interest, these studies can obtain adequate statistical power by following far fewer pregnant women than population-based cohort studies. To be useful for exposure cohort studies, pregnancy registries and teratogen information services must collect data from unexposed control pregnancies in the same manner as exposed pregnancies (Chambers et al., 1996, 2016). A few pregnancy registries and teratogen information services also collect data on the children in sufficient detail and with sufficient rigor to permit recognition of recurrent patterns of congenital anomalies (Cassina et al., 2012; Stadelmaier et al., 2017), something that is rarely possible in other kinds of epidemiology studies. Unfortunately, however, many pregnancy registry and teratogen information service data sets lack an appropriate internal control; they are essentially large case series. Statistical analysis of birth defect rates obtained from such studies using comparisons to rates obtained from meticulous population-based birth defects registries is inappropriate. In addition, women who call teratogen information services or who participate in voluntary pregnancy registries tend to be more affluent and healthier than the population as a whole (Lim et al., 2009; Kim et al., 2010) and may, therefore, be at lower risk of having babies with birth defects (Carmichael et al., 2003; Yang et al., 2007). Both population-based and exposure cohort studies can be used to estimate relative risk and statistical significance of associations that are observed, but insufficient statistical power may be a concern if the cohorts are not very large. The quality of the outcome data may also be an issue, especially if this information is obtained from the mother's, rather than the baby's, physicians. Like all observational studies, cohort studies may be subject to important biases and confounding if covariates and effect modifiers are not appropriately considered. Case–control studies compare the frequency of maternal exposures among children with a particular birth defect or other adverse outcome with the frequency of such exposures among unaffected children. This design usually provides greater statistical power for detecting associations between pregnancy exposures and birth defects than population-based cohort studies of an equivalent size, but case–control studies can only be used to look for associations with the particular outcome that is present in the cases. If a pregnancy exposure produces a different adverse outcome or a pattern of minor anomalies that is not included among the cases, the association cannot be detected. Case–control studies can be used to estimate relative risk and statistical significance of associations that are observed, but, because they may focus on very rare outcomes, statistically significant associations may be detected that have little clinical significance, even if they are causal. For example, an uncommon pregnancy exposure that doubled the risk of cyclopia from 0.00001 to 0.00002 but had no other teratogenic effect would not measurably increase the overall risk of serious birth defects among infants born of exposed pregnancies above the 2 to 3% (0.02 to 0.03) background expectation (Kucik et al., 2012; Feldkamp et al., 2017). The quality of the exposure data may also be an issue in case–control studies, especially if this information is obtained retrospectively from the mothers many months after the exposures occurred. Another important concern in studies that are based on large untargeted data sets is that case groups involving many different specific birth defects may be analyzed for associations with many different pregnancy exposures simultaneously, creating a “multiple comparisons” problem that is not resolvable without additional investigations (Goodman, 1998; Thompson, 1998). Case–control studies may also be subject to important biases and confounding if covariates and effect modifiers are not appropriately considered. The increasing availability of large sets of medical, pharmacy, administrative, vital statistics and birth defects registry data provides the opportunity to perform case–control, cohort or hybrid studies through electronic record linkage. As these large databases already exist, a record linkage study is usually much less expensive than collecting data specifically for a birth defects epidemiology study. On the other hand, if the data are collected for another purpose, such as billing, their quality for clinical teratology studies may be a serious concern, and information on potential confounders and effect modifiers is usually unavailable. Ecological studies test for associations between surrogate measures of exposure in groups of people and summary measures of adverse pregnancy outcomes in the groups. This method differs from most epidemiological studies, which test for associations between exposure and outcome in individual subjects. Ecological studies are usually relatively inexpensive because they are performed with data collected for other purposes, but consideration of confounding factors is often impossible because the analyses are done on populations rather than individuals. Ecological studies must be interpreted with great caution because associations observed in a group cannot necessarily be attributed to any particular member of the group: not all blue state voters are Democrats. Biological plausibility is a very useful consideration in some circumstances. For example, if an exposure is exclusively dermal and absorption through the skin does not occur, an exposure cannot plausibly harm the embryo. Biological plausibility can also be misleading if it is based on an incomplete understanding of possible teratogenic mechanisms. For example, one cannot conclude that a particular drug to which an embryo was exposed cannot be teratogenic because the drug's pharmacologic activity depends on a cellular receptor that is not expressed in the embryo. A teratogenic effect may have resulted from disruption of a mechanism that does not operate in adults but plays a critical role in normal embryonic development. Knowledge of the mechanism of action may help to determine whether a particular exposure is likely to have caused an infant's birth defects. Mechanism of action is likely to be invoked more often in causal inference in the future as our understanding of human developmental biology improves. Determining whether an exposure is teratogenic in humans requires evaluation of all available studies of the effects of that exposure during pregnancy, judgement of the quality and relevance of each study to the question at hand, and synthesis of these data into a coherent assessment that is consistent with current scientific understanding of the exposure and embryonic development. Computational biology has become an increasingly important tool in biomedical research, and it would be nice if there were a smart computer program that could make this determination for us. In toxicology, computational studies have generally endeavoured to predict toxic effects that occur in mammalian in vivo experiments from studies in simpler organisms or in vitro or in silico models (Ekins, 2014; Toropov et al., 2014; Mangiatordi et al., 2016). The application of computational toxicology to teratology and to predicting human effects from experimental data has been limited to date. Major challenges in this area are that the primary data from most teratology studies are not readily available to computational biologists throughout the world and that the teratogenic potential of only a small number of pregnancy exposures has been thoroughly studied in humans (Lo and Friedman, 2002; Adam et al., 2011). Much of the power of computational biology depends on open access to large comprehensive data sets, and these are not yet available for human developmental toxicology. Meta-analysis provides a systematic approach to synthesizing the results of epidemiology studies on a particular question. Meta-analysis sometimes allows quantitative conclusions that are not provided by any of a group of studies to be drawn when all of the studies are considered together. However, the quality of a meta-analysis is no better than the data in the individual studies, and meta-analysis is also subject to limitations inherent in the joint analysis. One issue of particular concern is that different birth defects epidemiology studies often use different definitions of exposure and outcome that may confound joint interpretation. In addition, studies that show an association between a maternal exposure during pregnancy and birth defects in the child are more likely to be published and cited than similar studies that do not show a statistically significant association (Koren and Nickel, 2011). Failure to include unpublished “negative” studies in a meta-analysis can distort the results. At present, expert consensus provides the most generally applicable method of inferring causality of a possible teratogenic effect in humans. An important advantage of this approach is that it can simultaneously evaluate studies of different types, sizes, and quality, including nonepidemiological studies. A major limitation is that expert consensus is qualitative, or, at best, semiquantitative. A rigorously quantitative conclusion cannot be provided, and the result cannot be tested statistically. Although subjective, an expert consensus must be seen as being authoritative to have value. The value depends critically on who is making the consensus and on the thoroughness, rigor, and transparency of their assessment. The participants must have the expertise needed to consider fairly, weigh appropriately and evaluate critically all relevant information that is available. If the purpose is to determine if a human pregnancy exposure is likely to cause an increased risk of adverse outcomes in infants, the assessment should be expressed in the context of likely exposure conditions. Moreover, an expert consensus is never more than a statement of opinion and is always provisional and subject to change if new or better information becomes available. Shepard's criteria (Shepard, 2010) (Table 2) provide a useful framework for expert consensus on the causality of an association that has been observed between a maternal exposure during pregnancy and birth defects in infants. Like the Bradford Hill criteria discussed above, Shepard's criteria should not be treated as a diagnostic algorithm but rather as a set of considerations for evaluating the available evidence. An example of the appropriate use of Shepard's criteria in this way is provided by a recent analysis by scientists at the U.S. Centers for Disease Control, which concluded that “a causal relationship exists between prenatal Zika virus infection and microcephaly and other serious brain anomalies” (Rasmussen et al., 2016). This consensus was achieved less than 1 year after the association was first suggested by alert clinicians (Oliveira Melo et al., 2016; Schuler-Faccini et al., 2016; Triunfol, 2016), when epidemiological data were still quite limited and no animal model of Zika virus embryopathy had yet been described. Subsequent research has confirmed that maternal Zika virus infection during pregnancy can cause microcephaly, severe brain disruption and associated neurological abnormalities in infants (Alvarado and Schwartz, 2017; Baud et al., 2017; Moore et al., 2017), but the fundamental research (Merfeld et al., 2017; Russo et al., 2017; Singh et al., 2017; Wen et al., 2017; Zhou et al., 2017) and public health measures (McCloskey and Endericks, 2017; Oussayef et al., 2017) undertaken before definitive epidemiology studies were completed probably prevented hundreds, if not thousands, of babies from suffering Zika virus embryopathy. Was short-cutting the Bradford Hill criteria and using expert consensus to declare that maternal Zika virus infection during pregnancy caused severe microcephaly “cheating”? Maybe, in a rigidly scientific sense, but it was the right thing to The Zika virus is an in recognition of a major teratogenic exposure in humans. was it For all of the (1) was a of a in (2) clinicians quickly something many babies were being born with a rare congenital (3) health were and assessed the The and needed to and to an of severe microcephaly had already been developed at and a few other and were and and and was to address the If we are serious about birth defects, we to be to exposure that is suspected of being teratogenic in humans in a similar manner and with the same This requires more and better surveillance and more and better hypothesis testing through case–control and cohort studies, experimental teratology studies, and In we greater to the scientific and public health and to identify and address the causes of birth defects that fewer babies are harmed of and of

Fetched live from OpenAlex and de-inverted. Abstracts are not stored in this database: the inverted indexes are 8.6 GB of the frame’s 9.3 GB of text, and the host has 13 GB free.