Reply to "reproducing Increased Dopamine with Infection to Evaluate the Role of Parasite-Encoded Tyrosine Hydroxylase Activity".

In their letter, McConkey et al. (1) suggest that differences in study design may have led to different results in our study compared with those of previous reports. In an effort to better understand these differences, we welcome the opportunity to provide more insight into the rationale for our study design and the reasoning behind the interpretations we reached. We stress at the outset that we had hoped to validate the previous findings that infection by Toxoplasma gondii leads to elevated dopamine production by dopaminergic cells in vitro and in chronically infected mice. In anticipation of such findings, we set out to disrupt the AAH2 gene, which had been implicated in this process by indirect data published previously by the McConkey group (2). Unfortunately, our studies failed to reproduce the original findings that infection increases dopamine production by using various parasite strains in different in vitro and in vivo models (3). In addition, review of the prior literature pertaining to the effects of T. gondii infection on elevated dopamine levels in vivo indicates that this pattern is highly variable (see points below). Because of the study design, the difficulties encountered in reproducing the original findings were not apparent until we had already generated the knockout and complement strains and begun testing them in parallel. This approach was chosen intentionally as an unbiased method for testing the hypothesis without a priori assumptions. We do not agree with the statement that it is essential to prove that our parental strain induces dopamine prior to engaging in gene knockout studies. Rather, our findings call into question whether the original findings are robust or generally reproducible. Although the letter by McConkey et al. suggests that our failure to observed elevated dopamine levels might be due to technical differences, we do not find this a compelling argument, as detailed in the following point-by-point response. (i) The authors claim that in their experiments, PC12 cells were kept competent to produce dopamine via attention to low passage number. We agree with the importance of this experimental detail. Our PC12 cells were expanded and frozen as low-passagenumber stocks shortly after being received from ATCC. In all experiments, cells were maintained for only 10 passages before being renewed from stock vials. (ii) The authors claim that our bradyzoite treatment, where we used high-pH growth medium to incubate infected PC12 cells, could quench dopamine production in these PC12 cells. Indeed, that is what we observed, a 25-fold decrease in total dopamine content produced by PC12 cells cultured under alkaline conditions. However, the result that was of interest to us was whether bradyzoites contribute to dopamine production in infected PC12 cells, as proposed by Prandovzsky et al. (2). If this prediction is correct, it stands to reason that the result should still hold even if dopamine production is globally lower. The fact that we still did not see a difference in overall dopamine content despite demonstrable evidence of differentiated bradyzoite-containing vacuoles inside PC12 cells challenges this hypothesis (3). (iii) The authors claim that their technique, soaking liberated tachyzoites in high-pH medium for 16 to 18 h and then infecting PC12 cells, differentiates the parasites into the bradyzoite stage without affecting the PC12 cells. We attempted to infect PC12 cells with bradyzoites that were liberated from high-pH-treated infected human foreskin fibroblast cells after 48 h, a time point when they stain positively for the Dolichos biflorus lectin (DBL), under conditions consistent with those of Prandovzsky et al. (2). However, at 48 h postinfection, the proportion of lectin-positive vacuoles was extremely low ( 12%). We expect that this resulted from parasites differentiating back into tachyzoites without continued pH stress to enforce the bradyzoite state. When we tried using high-pH treatment of extracellular parasites as reported by Prandovzsky et al. (2), we observed very poor viability, such that it was not possible to reliably infect PC12 cells. Hence, we modified the protocol to subject infected PC12 cells to high-pH medium, thereby inducing 100% DBL-positive vacuoles (i.e., bradyzoites). Under these conditions, we failed to see dopamine changes (3). (iv) The authors claim that in the absence of viability data, it cannot be excluded that the 25-fold dopamine decrease in alkaline PC12 cells could be due to cell death. PC12 cells were counted by light microscopy before being harvested into perchloric acid buffer for high-performance liquid chromatography, and the level of dopamine per 10 cells was determined on the basis of visual identification of intact cells. If alkaline treatment led to increased mortality of PC12 cells, this would be corrected for by this visual analysis. (v) The authors rightly point out that parasite strain differences might exist in the effects on dopamine and behavior and also point out that our strain, Pru ku80 hxg, has not been previously demonstrated to induce elevated dopamine prior to gene knockout. However, Pru ku80 hxg was not the only strain used in our study (3). We observed the same absence of dopamine change in vitro when using ME49 (unpublished data). In vivo, we demonstrated no change in brain dopamine not only in mice infected with Pru ku80 hxg but also in mice infected with ME49 and the original C56 strain used by Stibbs (4). Thus, the failure to observe