Heme’s relevance genuine? Re-visiting the roles of TANGO2 homologs including HRG-9 and HRG-10 in C. elegans

Reviewer #1 (Public review):

Summary:

Sandkuhler et al. re-evaluated the biological functions of TANGO2 homologs in C. elegans, yeast, and zebrafish. Compared to the previously reported role of TANGO2 homologs in transporting heme, Sandkuhler et al. expressed a different opinion on the biological functions of TANGO2 homologs. With the support of some results from their tests, they conclude that 'there is insufficient evidence to support heme transport as the primary function of TANGO2', in addition to their claims on the role of TANGO2 in modulating metabolism. While the differences are reported in this study, more work is needed to elucidate the biological function of TANGO2.

Strengths:

(1) This work revisited a set of key experiments, including the toxic heme analog GaPP survival assay, the fluorescent ZnMP accumulation assay, and the multi-organismal investigations documented by Sun et al. in Nature 2022, which is critical for comparing the two works.

(2) This work reported additional phenotypes for the C. elegans mutant of the TANGO2 homologs, including lawn avoidance, reduced pharyngeal pumping, smaller brood size, faster exhaustion under swimming test, and a shorter lifespan. These phenotypes are important for understanding the biological function of TANGO2 homologs, while they were missing from the report by Sun et al.

(3) Investigating the 'reduced GaPP consumption' as a cause of increased resistance against the toxic GaPP for the TANGO2 homologs, hrg-9 hrg-10 double null mutant provides a valuable perspective for studying the biological function of TANGO2 homologs.

(4) This work thoroughly evaluated the role of TANGO2 homologs in supporting yeast growth using multiple yeast strains and also pointed out the mitochondrial genome instability feature of the yeast strain used by Sun et al.

Weaknesses:

(1) A detailed comparison between this work and the work of Sun et al. on experimental protocols and reagents in the main text will be beneficial for readers to assess critically.

(2) The GaPP used by Sun et al. (purchased from Frontier Scientific) is more effective in killing the worm than the one used in this study (purchased from Santa Cruz). Is the different outcome due to the differences in reagents? Moreover, Sun et al. examined the lethality after 3-4 days, while this work examined the lethality after 72 hours. Would the extra 24 hours make any difference in the result?

(3) This work reported the opposite result of Sun et al. for the fluorescent ZnMP accumulation assay. However, the experimental protocols used by the two studies are massively different. Sun et al. did the ZnMP staining by incubating the L4-stage worms in an axenic mCeHR2 medium containing 40 μM ZnMP (purchased from Frontier Scientific) and 4 μM heme at 20 ℃ for 16 h, while this work placed the L4-stage worms on the OP50 E. coli seeded NGM plates treated with 40 μM ZnMP (purchased from Santa Cruz) for 16 h. The liquid axenic mCeHR2 medium is bacteria-free, heme-free, and consistent for ZnMP uptake by worms. This work has mentioned that the hrg-9 hrg-10 double null mutant has bacterial lawn avoidance and reduced pharyngeal pumping phenotypes. Therefore, the ZnMP staining protocol used in this work faces challenges in the environmental control for the wild type vs. the mutant. The authors should adopt the ZnMP staining protocol used by Sun et al. for a proper evaluation of fluorescent ZnMP accumulation.

(4) A striking difference between the two studies is that Sun et al. emphasize the biochemical function of TANGO2 homologs in heme transporting with evidence from some biochemical tests. In contrast, this work emphasizes the physiological function of TANGO2 homologs with evidence from multiple phenotypical observations. In the discussion part, the authors should address whether these observed phenotypes in this study can be due to the loss of heme transporting activities upon eliminating TANGO2 homologs. This action can improve the merit of academic debate and collaboration.

Reviewer #2 (Public review):

Summary:

This work investigates the roles of TANGO2 orthologs in different model systems and suggests bioenergetic dysfunction and oxidative stress (and not heme metabolism) as crucial pathways in TANGO2 deficiency disorders (TDD). Specifically, studies in C. elegans showed that the lack of TANGO2 ortholog activity (i) does not provide a survival benefit upon toxic heme exposure; (ii) results in a series of defects related to energy levels (reduced pharyngeal pumping, lawn avoidance, poor motility, and low brood size); (iii) reduces the fluorescence of the heme analog ZnMP in the intestine. Furthermore, upon oxidative stress, one TANGO2 ortholog, hrg-9, is upregulated compared to control conditions. Additional studies on yeast and zebrafish models failed to replicate prior findings on heme distribution and muscle integrity.

These findings have a clear therapeutic impact, as TDD currently has no cure but only symptom-managing treatments. Identifying the correct pathway to correct the disease is pivotal to finding a cure.

Although compelling, the authors' primary claim is based on indirect evidence that only hints toward it. Unfortunately, I do not see any direct and convincing evidence linking TANGO2 orthologs to bioenergetic and oxidative stress pathways.

Strengths:

(1) The study refutes and extends previous findings, highlighting new aspects of TANGO2's roles in cell physiology.

(2) The use of different model systems to address the main research questions is useful.

(3) The results suggest a broader impact than previously described, somewhat supporting the novelty of the study.

Weaknesses:

(1) The manuscript is written mainly as a criticism of a previously published paper. Although reproducibility in science is an issue that needs to be acknowledged, a manuscript should focus on the new data and the experiments that can better prove and strengthen the new claims.

(2) The current presentation of the logic of the study and its results does not help the authors deliver their message, although they possess great potential.

(3) The study is missing experiments to link hrg-9 and hrg-10 more directly to bioenergetic and oxidative stress pathways.

Reviewer #3 (Public review):

In this paper, Sandkuhler et al. reassessed the role of TANGO2 as a heme chaperone proposed by Sun et al in a recently published paper (https://doi.org/10.1038/s41586-022-05347-z) by partially repeating and failing to replicate experiments therein. Overall, Sandkuhler et al. conclude that the heme-related roles of TANGO2 had been overemphasized by Sun et al. especially because the hrg9 gene does not exclusively respond to different regimens of heme synthesis/uptake but is susceptible to a greater extent to, for example, oxidative stress.

In recent years, the discussion around the heme-related roles of TANGO2 has been tantalizing but is still far from a definitive consensus. Discrepancies between results and their interpretation are a testament to how challenging and ambitious the understanding of TANGO2 and the phenotypes associated with TANGO2 defects are. Overall, the work presented by Sandkuhler et al. in this manuscript challenges the recent developments in the field and promotes the continuous characterisation of TANGO2 in relation to heme homeostasis.

A few comments and questions:

(1) The authors stress - with evidence provided in this paper or indicated in the literature - that the primary role of TANGO2 and its homologues is unlikely to be related to heme trafficking, arguing that observed effects on heme transport are instead downstream consequences of aberrant cellular metabolism. But in light of a mounting body of evidence (referenced by the authors) connecting more or less directly TANGO2 to heme trafficking and mobilization, it is recommended that the authors comment on how they think TANGO2 could relate to and be essential for heme trafficking, albeit in a secondary, moonlighting capacity. This would highlight a seemingly common theme in emerging key players in intracellular heme trafficking, as it appears to be the case for GAPDH - with accumulating evidence of this glycolytic enzyme being critical for heme delivery to several downstream proteins.

(2) The observation - using eat-2 mutants and lawn avoidance behaviour - that survival patterns can be partially explained by reduced consumption, is fascinating. It would be interesting to quantify the two relative contributions.

(3) In the legend to Figure 1A it's a bit unclear what the differently coloured dots represent for each condition. Repeated measurements, worms, independent experiments? The authors should clarify this.

(4) It would help if the entire fluorescence images (raw and processed) for the ZnMP treatments were provided. Fluorescence images would also benefit Figure 1B.

(5) Increasingly, the understanding of heme-dependent roles relies on transient or indirect binding to unsuspected partners, not necessarily relying on a tight affinity and outdating the notion of heme as a static cofactor. Despite impressive recent advancements in the detection of these interactions (for example https://doi.org/10.1021/jacs.2c06104; cited by the authors), a full characterisation of the hemome is still elusive. Sandkuhler et al. deemed it possible but seem to question that heme binding to TANGO2 occurs. However, Sun et al. convincingly showed and characterised TANGO2 binding to heme. It is recommended that the authors comment on this.

Author response:

We have reviewed the helpful feedback from the reviewers and would like to thank them for their careful consideration of our manuscript. By way of provisional response, we agree with many of the above points and plan to revise our manuscript accordingly.

In an effort to replicate some of the heme trafficking-related experiments in the original paper using a C. elegans model of TDD, we were either unable to do so or demonstrated an alternative explanation for the findings we could partially reproduce. As the reviewers correctly point out, there were some methodological and reagent-related differences between the study by Sun et al. and our own that we will more directly highlight in a subsequent manuscript version. Additionally, where possible, we will attempt to replicate these experiments using the same protocol(s).

We observed several phenotypic traits observed in the C. elegans model of TDD that were not previously described in prior studies. While we believe these features to be consistent with a bioenergetic problem in the worm, direct evidence for this is admittedly lacking in our original manuscript. We are actively engaged in experiments examining potential functions of HRG-9 and HRG-10 unrelated to heme trafficking and will consider which data best aligns with the scope of this study, thus warranting inclusion in a subsequent manuscript version. We will also provide a more comprehensive review of relevant data generated by other groups (e.g., lipid dysregulation, impaired autophagy, mitochondrial dysfunction in the absence of TANGO2) in the discussion section.

Recommended improvements related to figure legends, terminology, and formatting will also be executed in our forthcoming version. On behalf of my co-authors and myself, thank you again for your time and effort improving this work.