Organophosphorus Pesticide Exposure at 17 Weeks’ Gestation and Odds of Offspring Attention-Deficit/Hyperactivity Disorder Diagnosis in the Norwegian Mother, Father, and Child Cohort Study

Round 1

Reviewer 1 Report

The authors of this paper apply their significant epidemiological expertise, substantial longitudinal data, and a sophisticated statistical plan to a fatally flawed analysis.  The author use a single measure of pesticide dose (organophosphorus pesticide urinary metabolites at 17 weeks gestation) to predict ADHD in children.  They conclude that pre-natal exposure to organophosphorus insecticides is not related to a childhood ADHD diagnosis based on this single exposure data point.  They ignore the fact that OPs are non-persistent pesticides that are metabolized and excreted within 24 to 72 hours after exposure.  OP dose varies from hour to hour after exposure.   One data point does not indicate how often a fetus is exposed or the dose received across the 36 weeks of gestation, during infancy, or during early childhood.

 

This analysis is analogous asking whether that a child who shoplifts at age 6 years will be a hardened criminal as an adult.

 

In addition to bad science, this fatally flawed study has policy and public health implications.  These types of results are used by pesticide manufacturers and industrial agriculture to justify the continued use of hazardous neurotoxicants for which safety data is not made available.

Author Response

Please see the attachment.

Author Response File: Author Response.docx

Reviewer 2 Report

General comments

This is a well-written manuscript reflecting an interesting research approach. I find it very important to publish also studies that do not elucidate an additional hazard or risk linked to OPs at least in a country in which most people consume residues in the diet but are not directly exposed by spraying. In this paper, there is little to do for the reviewer and, accordingly, I have only very few questions, remarks or suggestions for possible improvement.

Specific comments

Introduction

Lines 61 - 65: The correctly described acute mode of action (in insects) is just the reason for toxicity also to non-target organisms. The word "however", to me, suggests a different mechanism which is not true. Perhaps you could think about revising the wording a bit.

Line 78: What is meant here? Exposure of children or of their mothers/parents? Please clarify!

Line 79: Should the word "and" perhaps replaced by "in" (performance-based measures)?

Material and methods, Statistical analysis:

Lines 220-223, also 230-231: I must confess not to fully understand what is meant with "potential co-pollutant confounding". Is it exposure to other OPs not included in the analysis? To me, the whole desription of "other OP molar sum" is not that clear and should be explained in a bit more detailed way. (Don't take me wrong: I don't doubt your approach but I have just difficulties to understand it and other readers could feel the same.)

Results

No comments.

Discussion

(1) I have got the impression that the percentage of affected children (i.e. those with ADHD diagnosis) is rather low in the Norwegian population under examination (297 cases in an eligible population of 24,035 according to the introduction, i.e., slightly more than 1.2%). This is a much lower rate than 3 - 6% as given in the first sentence of the introduction as the worldwide estimate. Any explanation for that and is this observation worth noting in the discussion?

(2) The urine sampling in gestation week 17 is, correctly, discussed as one of the (few) limitations because of the fast metabolism of OPs (lines 101-104). Accordingly, the measurements might be not representative for exposure during the whole gestation period (even though I think that they are). But what about (hypothetical) differences in the "windows of sensitivity" to a possible impact of OPs, or other xenobiotics, during gestation that may have an impact on the postnatal phenotypic expression of clinical entities with a strong hereditary background in children (as to assumed also for ADHD)?

 

Author Response

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Author Response File: Author Response.docx

Reviewer 3 Report

The manuscript by Hall et al evaluated associations of several organophosphorus pesticides (OPs) with ADHD diagnosis in the Norwegian MoBa cohort. Authors did not find evidence of a meaningful association between OPs and ADHD overall or when considering sex-specific associations. This was a well-conducted study with appropriate methodology and interpretation. Some minor recommendations for improvement or consideration are below:

 

1.     Could authors provide context for exposure distributions in this cohort compared to others? Levels in the U.S. may or may not be relevant, but it would be helpful to know whether these concentrations are generally “high” or “low”. This information can be included in the abstract/introduction and perhaps discussed in the results if comparison values are available to complement Table 2.

2.     Lines 165-166: Please provide % below the LOD (or detectable) for each analyte.

3.     Line 170: Please provide the equation for each SG conversion (including molar mass).

4.     Lines 170: Could authors provide justification for summed measures? Does it make sense to also consider single-metabolite analyses?

5.     Information related to confounders in lines 197-202 and 217-226: Could this information be streamlined and reported together in one section? There are some (understandable) differences in the listed covariates, so it would be helpful to report the process more systematically. Related: the DAG MSAS did not include maternal ADHD diagnosis but the final model did?

6.     Line 205: Could authors briefly mention that missingness is reported in Table 1? It is described later but would be helpful to reference here.

7.     Line 221-222: given the moderate correlation between some OPs, is there concern for multicollinearity when including several OPs in one model? Would a statistical mixture approach help with this?

8.      Table 2: Could GM and SD be reported in one column? GM (SD), followed by the % distributions in subsequent columns.

9.     Page 1, last paragraph of results (no line numbers): The presence of a “significant” EMM is not necessarily critical to interpret sex-specific associations as long as patterns are discussed, as authors have done, especially in a study with relatively small (stratified) sample sizes. However, it seems a bit belated to highlight the EMM results at the end of the paragraph when sex-specific associations have already been discussed above. Would recommend stating the lack of EMM first and then continuing on to discuss the sex-specific results.

10.  Findings in Table 3: Authors thoughtfully explained how they came to the decision to consider OPs in tertiles; however, given the relatively small sample size of the study, could other approaches be considered for modeling exposure? Could authors consider additionally reporting associations using continuous OP variables? There seems to be some evidence of non-linearity, but it isn’t very obvious.

11.  Discussion, first sentence: Although MoBa is large, the nested study has a (comparatively) small sample size, especially to evaluate sex-stratified associations (where there appeared to be some potential for meaningful findings). This may need to be discussed in the strengths/limitations section.

Author Response

Please see the attachment.

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report

None — I am traveling through the middle of January and cannot review this revision.