DDT and Urogenital Malformations in Newborn Boys in a Malarial Area

The October 22, 2009 paper by Bornman, et al., reports urogenital birth defects (UGBDs) in South Africa as a result of DDT exposure. After obliquely inferring DDT may not be the actual cause of the observed birth defects, the authors asserted that people at risk of malaria should be informed about risks of birth defects if DDT is used. The popular media in South Africa publicised the authors' claims widely, to include rural malarial areas. Public concern has arisen, and as a consequence the malaria control program is encountering new obstacles.

Most people would agree that because DDT provides great benefit by protecting people from malaria and other diseases, it does not make sense to alarm people about DDT unless it has been proven to cause harm. Richard Grady addressed this issue in the editorial comment that accompanied the Bornman, et al., paper. Grady stated that issues of association and causality could not be distinguished in the paper. Given that there are broadly accepted epidemiological criteria, which are described below for defining causation, Grady was right. The claim that DDT causes birth defects does not fulfill any of these criteria and, based on the science, the pronouncement that there is an urgent need to warn people in malarious areas that they are at risk of birth defects if DDT is used, should not have been published. In addition to this destructive and alarmist pronouncement, herein specific examples of selective bias and misrepresentations of science will be described.

Firstly, it is important to consider some basic issues of DDT dosing and availability. Presence of DDT in living organisms is largely confined to fat cells where it is not biologically active. Thus, dosing in in vitro studies should account for differences in actions of chemical from acute dosing versus chemical stored in fat cells. Additionally, dosing on the basis of chemical concentrations in blood serum must differ between estimates of unadjusted (ng/mL) versus adjusted concentrations (ng/g lipid).

Most people would agree that because DDT provides great benefit by protecting people from malaria and other diseases, it does not make sense to alarm people about DDT unless it has been proven to cause harm.

The former measurement can give estimated concentrations far more than a hundred-fold less than the latter. This occurs because DDT and its metabolites are in the lipid fraction of blood serum, which comprises only about 0.6% of serum. A 1991 paper classified serum DDT levels in South Africa for people living in DDT sprayed houses as very high (unadjusted concentrations of 140 µg/L). In reality, that level equates to just 0.14 ppm of sum DDT (1 µg/L = 1 ppb and (µg/L)/1000 = ppm). Compare that "high" level with the concentrations used in animal tests below.

In making their case against DDT as a cause of human birth defects, Bornman and co-authors make several claims from published literature that warrant further consideration. They cite a paper by Kelce, et al., and state p,p'-DDE inhibits androgen binding, androgen-induced transcriptional activity, and normal male prepubertal development. They cite a paper by Danzo as demonstrating p,p'-DDE was the most potent of chemicals tested at binding androgen. Bornman and co-authors failed to state that neither of these studies involved humans. The study by Kelce, et al., was on rats and the investigators dosed rats with 100 to 200 mg/kg/day of DDE. For comparable dosing of a 68 kg human, such dosage levels would equate to a daily administration of 7,000 to 14,000 mg of DDE. In the real world, a comparable acute dose of DDE would never be present in a sprayed house, let alone be available in a form that could be consumed daily by a human living in the house. The paper by Danzo consisted of laboratory assays of physiological ligands and the tests were dosed with 100 µmol of DDT, DDE, etc., and with just 7 nmol of ligand. In reality, 100 µM of DDT equates to an in vitro concentration of about 35 ppm, so the investigators used unrealistically high doses of DDT versus miniscule concentrations of ligand. The point of these examples is that Bornman and co-authors imply these observations are relevant to humans. In fact, the observations are not relevant to humans because they are performed with rats or are in vitro tests. Additionally, the observations are based on extraordinarily high acute doses of DDT that humans will not normally, if ever, encounter. Indeed, Danzo specifically stated "Whether these compounds would act in vivo [in living organisms] as agonists or antagonists of androgen action remains to be determined."[4]

Bornman and co-authors describe the damage of in utero exposure of animals to DDT or DDE. They state such exposures are associated with reduced penis size in alligators, and hypospadias and cryptorchidism. For the claim of reduced penis size in alligators, they cite a paper by Guillette, et al. In fact, the authors (Guillette, et al., 1999) actually renounce the claim in that paper, stating:

"[a] recent study from our laboratories demonstrated no relationship between plasma concentrations of various pesticide metabolites and phallus size in juvenile male alligators from Lake Apopka, suggesting that an activational antiandrogenic response to the contaminants studied may not explain phallus size [cite removed]. It is important to note that we still have no data on which, if any, of the pesticides present in alligator tissues act as antiandrogens."

Bornman and co-authors also refer to a paper by De Jager, et al., for their statement that in utero exposure of animals to DDT causes hypospadias and cryptorchidism. In a similar fashion, their statement is wrong because the paper (De Jager, et al., 2006) was not about in utero exposure of animals to DDT. Collectively, their claims reflect, at worst, a purposeful misrepresentation of science, or, at best, a failure to read the literature.

In addition to the problems of interpretation and representation of cited literature, the Bornman, et al., paper also includes several inconsistencies and shortcomings in design, data analyses and interpretation. Bornman and co-authors find an association and then claim that they have found cause and effect. To prove a claim about DDT's impact on human health, researchers should satisfy the criteria for proving a cause and effect relationship. These criteria are: 1) Strength of association-–the stronger an observed association appears over a series of different studies, the less likely this association is spurious because of bias; 2) Dose-response effect--the value of the response variable changes in a meaningful way with the dose (or level) of the suspected causal agent; 3) Lack of temporal ambiguity--the hypothesized cause precedes the occurrence of the effect; 4) Consistency of the findings--most, or all, studies concerned with a given causal hypothesis produce similar findings; 5) Biological or theoretical plausibility--the hypothesized causal relationship is consistent with current biological or theoretical knowledge; 6) Coherence of the evidence--the findings do not seriously conflict with accepted facts about the outcome variable being studied; 7) Specificity of the association--the observed effect is associated with only the suspected cause (or few other causes that can be ruled out).

The study by Bornman and co-authors fails to satisfy these criteria. Furthermore, other studies already exist that are not consistent with the authors' findings of DDT as a cause of UGBDs., Claiming a cause and effect relationship on the basis of an observational study, such as the one by Bornman and co-authors, is not appropriate. History has shown that once a claim of causation is made, over the next several years other studies are performed and that claim is often rejected. This sequence has been repeated with such frequency that it should now be well understood that a correlation between variables, as might result from a cross-sectional study, does not prove causation. Yet, many investigators still succumb to temptation and claim their research proves more than it actually does. In the case of DDT, this has occurred over and over again with such ills as reduced duration of lactation, various cancers, birth defects, etc. For example, DDT as a cause of reduced duration of lactation was announced in 1985. This claim was followed by other studies, eventually leading to a 2003 high-profile suggestion in infectious disease literature that DDT might be too harmful for use in malaria control. Years later, in 2008, a large study disproved that DDT caused reduced duration of lactation. Another example was the claim that DDE caused breast cancer. Anti-DDT activists used the reported association of DDE with breast cancer to campaign against public health use of DDT. A meta-analysis of many studies in 2004 disproved DDE was a cause of breast cancer. A highly damaging part of this cyclic process is that the media report the initial claim but ignore later studies that disprove the original claim of causation. Indeed, as described above, the media in South Africa has widely reported claims of the Bornman, et al., paper as proof that DDT causes birth defects and to the detriment of the malaria control program.

In addition to the issues described above, inconsistencies in the data used should give serious cause for concern. Bornman and co-authors state that the final dataset for computations consisted of 3310 newborn baby boys. However in Table 1, the summed total of boys listed by maternal age is 3304; the summed total of boys listed by maternal occupation is 3253; and the summed total of boys listed by ethnicity is 3310. Such differences would be irrelevant if differences in UGBDs within exposed and unexposed populations were large; but they were not. The differences in the summed totals of these characteristics are unexplained, and given these differences, it is unclear which denominator values were used in estimating the distribution of UGBDs in Table 3.

The authors state that the final multivariate logistic model included only 3144 baby boys. If the authors started with 3310 boys, which boys expressing which UGBDs were dropped out of the model in order to get a combination of UGBDs to give a significant model? Such changes in the population would perhaps be less important if investigators had employed a rigorous statistical standard for admitting parameters into the model in the first place. However, instead of the standard 0.05 probability level, they used a p-value of 0.15. The authors explain how they arrived at a total sample size of 3310 boys, but do not explain which boys were dropped out of the model to arrive at a final sample size of 3144 boys.

Other inconsistencies are found in Table 3. The values listed for "any UGBD" are undefined and are less than the summed total of the six UGBDs in the corresponding column. Table 3 consists of values for six UGBDs in three columns, including "n", "ever sprayed," and "never sprayed." The summed total of the six UGBDs for the columns "ever sprayed" and "never sprayed" are 300 and 97 respectively. The last row of data is "any UGBD." It would be expected that the values in this row would be equal to or greater than the summed total of the six UGBDs in the corresponding column (i.e. 300 and 97; but instead the values are 264 and 93 respectively). Since the authors refer to this row as representing "any UGBD," the values could include some conditions not described in the list of six UGBDs. But the values for "any UGBD" are actually fewer than the summed totals of the six UGBDs. The authors state in their text that any category with a count less than five would be excluded; therefore, since the values for "penile cyst" were less than five, these were subtracted from the summed totals to determine if the differences were due to the deletion of this data. Subtracting the values (3 and 4) for "penile cyst" however does not account for the differences between the summed totals of the six UGBDs and the values listed for "any UGBD."

The threshold for statistical significance of a cause and effect relationship (p-value equal to or less than 0.15) is set well below what is considered acceptable (p-value equal to or less than 0.05). The authors do not appear to understand that the 95% confidence interval is a useful approximation of statistical significance for a cause-effect relationship only when the odds ratio is large and widely separated from 1.0. Data presented in this study do not suggest that such relationships exist. One can, in general, interpret a 0.05 level of significance as suggesting that, for a set of 20 parameters, at least one can be expected to show a p-value less than or equal to 0.05. That is to say, the chance of getting a result that is due to chance alone is 1 in 20. In this study, the authors set their p-value at 0.15. Thus, the probability of getting a result that is due to chance is 1 in 6.7. The authors worked with multiple variables and outcomes, so the chance that an association will be significant at the 0.15 level of probability is high—chance being 1 in 7. Lowering statistical standards for finding a significant correlation is not good statistical practice; it is particularly unacceptable when an erroneous conclusion may cause harm. In such circumstances, statistical standards should be raised, not lowered.

The percentage of UGBDs in villages never sprayed with DDT is high at 10.2%, and not significantly different from the 11% observed in villages sprayed with DDT. Given the high percentages of UGBDs in both DDT-sprayed and unsprayed communities, research should be undertaken to determine the cause. Yet, it seems clear that a focus on DDT will divert attention away from the real cause(s) and, simultaneously, increase the risk that DDT will be withdrawn from the malaria control program in South Africa. It was withdrawn once before with disastrous consequences and would be a great public disservice if the Bornman, et al., paper was the cause of a repeat performance of that disaster.

It seems clear that the Bornman, et al., paper itself now poses great risks to the health and welfare of people in malarious areas because it may become the cause célèbre for stopping house spray programs that use DDT.

Roger Bate is the Legatum Fellow in Global Prosperity at AEI.

Notes

  1. Bornman R, de Jager C, Worku Z, Farias P, Reif S. DDT and urogenital malformations in newborn boys in a malarial area. BJU Int 2009; doi:10.1111/j.1464-410X.2009.09003.x
  2. Bouwman H, Cooppan RM, Becker PJ, Ngxongo S. Malaria control and levels of DDT in serum of two populations in Kwazulu. J Toxicol Environ Health 1991; 33(2): 141-55
  3. Kelce WR, Stone CR, Laws SC, Gray LE, Kemppainen JA, Wilson EM. Persistent DDT metabolite p,p'-DDE is a potent androgen receptor antagonist. Nature 1995; 375(6532): 581–5
  4. Danzo BJ. Environmental xenobiotics may disrupt normal endocrine function by interfering with the binding of physiological ligands to steroid receptors and binding proteins. Environ Health Perspect 1997; 105(3): 294–301
  5. Guillette LJ Jr, Woodward AR, Crain DA, Pickford DB, Rooney AA, Percival HF. Plasma steroid concentrations and male phallus size in juvenile alligators from seven Florida Lakes. Gen Comp Endocrinol 1999; 116(3): 356–72
  6. de Jager C, Farias P, Barazza-Villarreal A, Avila MH, Ayotte P, Dewailly E, et al. Reduced seminal parameters associated with environmental DDT exposure and p,p'-DDE concentrations in men in Chiapas, Mexico: a cross-sectional study. J Androl 2006; 27(1): 16–27
  7. Bhatia R, Shiau R, et al. Organochlorine pesticides and male genital anomalies in the child health and development studies. Environ Health Perspect 2005; 113(2): 220-224
  8. Longnecker MP, Klebanoff MA, et al. Maternal serum level of 1,1-dichloro-2,2-bis(p-chlorophenyl)ethylene and risk of cryptorchidism, hypospadias, and polythelia among male offspring. Am J Epidemiol 2002; 155(4): 313-22
  9. Rogan WJ, Gladen BC. Study of human lactation for effects of environmental contaminants: the North Carolina Breast Milk and Formula Project and some other ideas. Environ Health Perspect 1985; 60: 215-221
  10. Chen A, Rogan WJ. Nonmalarial infant deaths and DDT use for malaria control. Emerg Infect Dis 2003; 9(8): 960-4
  11. Cupul-Uicab LA, Gladen BC, Hernandez-Avila M, Weber JP, Longnecker MP. DDE, a degradation product of DDT, and duration of lactation in a highly exposed area of Mexico. Environ Health Perspect 2008; 116(2): 179-83
  12. Wolff MS, Toniolo PG, Lee EW, Rivera M, Dubin N. Blood levels of organochlorine residues and risk of breast cancer. J Natl Cancer Inst 1993; 85(8): 648-52
  13. Lopez-Cervantes M, Torres-Sanchez L, Tobias A, Lopez-Carrillo L. Dichlorodiphenyldichloroethane burden and breast cancer risk: a meta-analysis of the epidemiologic evidence. Environ Health Perspect 2004; 112(2): 207-14
  14. A Google search of news stories published around the time the Bornman, et al., paper was released produced over 20 print and electronic hits. These included the most widely read and popular newspapers in South Africa. In addition, an investigative journalism television program gave wide coverage to the research. Coverage was also given via radio, which is particularly important for rural areas. None of the popular media stories questioned the findings or methodology of the study. Only 2 news stories were found that discussed the relative risk of malaria infection, making the point that the benefits of DDT spraying may outweigh the risks of DDT to human health.

Photo Credit: iStockphoto/Antonio Nunes

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About the Author

 

Roger
Bate
  • Roger Bate is an economist who researches international health policy, with a particular focus on tropical disease and substandard and counterfeit medicines. He also writes on general development policy in Asia and Africa. He writes regularly for AEI's Health Policy Outlook.
  • Phone: 202-828-6029
    Email: rbate@aei.org
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