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On 2015 Aug 05, Roger H Reeves commented:

Response to Benoit Bruneau (Bruneau’s comments in italics)

Bruneau: The paper by Polk et al purports to demonstrate a genetic interaction between Tbx5 and Ts65Dn. I have a number of comments and questions related to the data used to reach this conclusion. First, the reduced amount of Tbx5 in the Ts65Dn is interesting, but puzzling is the almost complete absence in the Ts65Dn;Tbx5+/- embryos: based on previous investigations, this level of Tbx5 mRNA (almost zero) should result in extremely severe defects in heart formation, which are not observed.

Response: We show a qPCR analysis at a single developmental time point, the E12.5 heart. Although continuous low Tbx5 levels beginning earlier in heart development would result in severe heart defects as Bruneau suggests, the ramifications of diminished expression at E12.5 are unclear. Perhaps the increased lethality in Ts65Dn;Tbx5+/- mice is related to this observation. In an unnecessary ad homonym attack, Bruneau intimates that we are incapable of using qPCR appropriately (“This brings into question the quantitation of the mRNA levels”). Instead, it is Bruneau’s supposition that our observation at E12.5 could only be accurate if severe heart malformations were observed which is incorrect.

Bruneau: Data are presented only for 2 of the 4 genotypes that would be necessary to derive any conclusion [about genetic association]. In table 3, WT and Ts65Dn genotypes are not present. In Figure 2, only the compound heterozygote Ts65Dn;Tbx5+/- and WT are shown.

Response: The expected frequencies for these defects in wt and Ts65Dn mice have been published multiple times by us and others and three relevant studies are cited [1-3] showing that in a sample of this size, we would expect to see <1 ASD, <1 VSD, 0 AVSD and 0 OA in the same genetic background as this study. That is, we would expect to observe few or no defects and the same for wt. Perhaps we could have made a more concrete reference to the cited studies with regard to this specific point; however, neither we nor the reviewers found our presentation to be problematic. Even for those who missed the reference, we disagree with the statement that there is “no evidence [in Table 3] for genetic interaction.” The combination of genotypes unequivocally changes the phenotype; what forces not involving genetics might be responsible?

Bruneau: The same genotypes are missing from Fig 4.

Reponse: Fig. 4 is a histological representation. Since the defects don’t occur and such controls in the same genetic background have already been published, we choose to cite them rather than reproduce them here.

Bruneau: The in situ hybridization in Fig 4 suggests a reduction in Pitx2 expression in Ts65Dn;Tbx5+/- hearts; despite a very weak signal, this may be true, but this in no way indicates that the mice have atrial isomerism nor that the left-right pathway is involved in the defects shown.

Response: Here Bruneau overstates our conclusions about left-right patterning in order to criticize them (straw man argument). We show that OA incidence increases in Tbx5;Ts65Dn mice (Tbl. 3) – Bruneau tacitly agrees. We show that Pitx2 expression is lower in LA of Ts65Dn – Bruneau agrees with this as well. We discuss our findings in the context of the literature on OA where one finds frequent references to the relationship between OA and left-right development of the heart (see 12 references to the relationship between OA, Pitx2 and left-right signaling, 2nd paragraph of the Discussion). We point out the established link between altered patterns of Pitx2 expression, left-right isomerism and OA as a justification for doing this experiment in Fig 4 with the results shown. However, we do not state that OA is due to atrial isomerism, nor do we state that any of these mice have atrial isomerism. Bruneau has misstated our conclusion.

Bruneau: The atria of the mutant mice (in Fig 4) clearly have their normal morphology

Response: We note that it is not possible to correctly deduce complex pathological relationships from a single histological image. Regardless, it is irrelevant, as we do not assert that left-right isomerism is observed; that is a straw man of Bruneau’s invention.

Bruneau: I look forward to reading the authors' responses to these issues.

Response: We expect differences of opinion in interpretation by experts as a useful and necessary part of the scientific enterprise. Here, however, Bruneau has offered a superficial and needlessly aggressive critique replete with mischaracterization of our stated conclusions. We trust that objective readers interested in the complex phenomena resulting in heart defects in Down syndrome will consider our data for its intrinsic value and not mischaracterize our qualified speculations in the Discussion as conclusions.

Signed: Roger Reeves, Renita Polk, Peter Gergics, Ivan Modkowitz and Sally Camper

1. Moore CS (2006) Postnatal lethality and cardiac anomalies in the Ts65Dn Down syndrome mouse model. Mamm Genome 17: 1005-1012.
2. Williams AD, Mjaatvedt CH, Moore CS (2008) Characterization of the cardiac phenotype in neonatal Ts65Dn mice. Dev Dyn 237: 426-435.
3. Li H, Cherry S, Klinedinst D, DeLeon V, Redig J, et al. (2012) Genetic modifiers predisposing to congenital heart disease in the sensitized Down syndrome population. Circ Cardiovasc Genet 5: 301-308.

On 2015 Jul 29, Benoit Bruneau commented:

The paper by Polk et al purports to demonstrate a genetic interaction between Tbx5 and Ts65Dn. I have a number of comments and questions related to the data used to reach this conclusion. First, the reduced amount of Tbx5 in the Ts65Dn is interesting, but puzzling is the almost complete absence in the Ts65Dn;Tbx5+/- embryos: based on previous investigations, this level of Tbx5 mRNA (almost zero) should result in extremely severe defects in heart formation, which are not observed. This brings into question the quantitation of the mRNA levels. This is very minor point compared to the presentation of the data: data are presented only for 2 of the 4 genotypes that would be necessary to derive any conclusion. In table 3, WT and Ts65Dn genotypes are not present. In Figure 2, only the compound heterozygote Ts65Dn;Tbx5+/- and WT are shown; how can one judge any genetic interaction if the individual genotypes (Ts65Dn and Tbx5+/-) are not shown? In certain genetic backgrounds we see such defects occasionally in Tbx5+/- neonates, therefore the conclusions proposed by the authors cannot be reached with the data provided. The same genotypes are missing from Fig 4. The in situ hybridization in Fig 4 suggests a reduction in Pitx2 expression in Ts65Dn;Tbx5+/- hearts; despite a very weak signal, this may be true, but this in no way indicates that the mice have atrial isomerism nor that the left-right pathway is involved in the defects shown. The atria of the mutant mice clearly have their normal morphology, and there is no evidence presented of isomerism (e.g. ectopic or missing sinoatrial node, abnormal venous valve connections), not are any left-right pathway components (upstream or downstream of Pitx2) explored. The authors' conclusions regarding overriding aorta as a product of defective LR asymmetry, especially that of the atria, is particularly puzzling, as these are opposite poles of the heart. Therefore the conclusions related to disruption of left-right pathways in this genotype is not at all supported. I look forward to reading the authors' responses to these issues.

On 2015 Jul 29, Benoit Bruneau commented:

The paper by Polk et al purports to demonstrate a genetic interaction between Tbx5 and Ts65Dn. I have a number of comments and questions related to the data used to reach this conclusion. First, the reduced amount of Tbx5 in the Ts65Dn is interesting, but puzzling is the almost complete absence in the Ts65Dn;Tbx5+/- embryos: based on previous investigations, this level of Tbx5 mRNA (almost zero) should result in extremely severe defects in heart formation, which are not observed. This brings into question the quantitation of the mRNA levels. This is very minor point compared to the presentation of the data: data are presented only for 2 of the 4 genotypes that would be necessary to derive any conclusion. In table 3, WT and Ts65Dn genotypes are not present. In Figure 2, only the compound heterozygote Ts65Dn;Tbx5+/- and WT are shown; how can one judge any genetic interaction if the individual genotypes (Ts65Dn and Tbx5+/-) are not shown? In certain genetic backgrounds we see such defects occasionally in Tbx5+/- neonates, therefore the conclusions proposed by the authors cannot be reached with the data provided. The same genotypes are missing from Fig 4. The in situ hybridization in Fig 4 suggests a reduction in Pitx2 expression in Ts65Dn;Tbx5+/- hearts; despite a very weak signal, this may be true, but this in no way indicates that the mice have atrial isomerism nor that the left-right pathway is involved in the defects shown. The atria of the mutant mice clearly have their normal morphology, and there is no evidence presented of isomerism (e.g. ectopic or missing sinoatrial node, abnormal venous valve connections), not are any left-right pathway components (upstream or downstream of Pitx2) explored. The authors' conclusions regarding overriding aorta as a product of defective LR asymmetry, especially that of the atria, is particularly puzzling, as these are opposite poles of the heart. Therefore the conclusions related to disruption of left-right pathways in this genotype is not at all supported. I look forward to reading the authors' responses to these issues.