expression of concern https://www.science.org/doi/10.1126/sciadv.aeb2713

On 17 November 2021, Science Advances published the Research Article “Discovery of anti-inflammatory physiological peptides that promote tissue repair by reinforcing epithelial barrier formation” by Y. Oda et al. (1). The authors informed the journal of an institutional investigation related to the experimental conditions used for Fig. 2B. We are notifying readers while the institution reviews these issues.

I would like to ask the authors about an apparent inconsistency between the survival curve shown in Fig. 4I of this paper and the graph reconstructed from the raw Excel data uploaded to Zenodo(GitHub).

Zenodo (10.5281/zenodo.5525680) (GitHub)

In addition, the experiments shown in Fig. 4H and 4I are described in the manuscript as having been performed according to the statement: “consecutive administrations of JIPm35 starting at 4 days after DSS treatment, when the mice had manifested the bloody feces symptom.” However, this statement also does not appear to be consistent with the raw Excel data.

First, regarding the discrepancy in the reconstructed graph for Fig. 4I, the Excel file itself contains a different number of mice than reported in the Materials and Methods section of the paper. Specifically, mice exceeding the stated n = 6 were present in the DSS (n = 7) and DSS+JIPm35 (n = 8) groups, and these animals appear to have been excluded from the published analysis.

No exclusion criteria are described in the paper; the Materials and Methods section and the figure caption merely state n = 6.

When I reconstructed the graph using the same method as the authors without excluding any mice, both the shape of the Kaplan–Meier survival curves and the statistical results changed. In particular, the significant differences reported in the original paper for DSS+vehicle vs DSS+JIP and DSS+JIP vs DSS+JIP-mut1 were no longer observed.

Furthermore, in order to determine whether the original statistical results could be reproduced, I also reconstructed the graph by excluding mice in exactly the same manner as the authors. Even under these conditions, part of the published graph still could not be reproduced.

I would appreciate the authors’ response regarding these concerns.

Dear Authors,

In addition to the concerns raised above regarding the survival curves in Fig. 4I, a similar pattern of inconsistency appears to be present in the body weight loss data shown in Fig. 4H. According to the Materials and Methods, both the survival analysis and the body weight assays were performed with n = 6. However, in the body weight graph, the number of mice per group appears to decrease from n = 6–8 to n = 4, suggesting that certain animals were excluded. I was unable to identify any description of the exclusion criteria in the manuscript, and I would be grateful if you could clarify where these criteria are specified.

Furthermore, reconstruction of the body weight curves from the raw data, as in the case of the survival curves, did not reproduce the published results correctly. I also reconstructed the curves without excluding animals (using n = 6, consistent with the survival analysis, in line with the authors’ description). In neither case was I able to obtain the reported statistical significance (p < 0.001). Could you please clarify under which conditions the Kruskal–Wallis test was performed?

Finally, I also analyzed the mice that appear to have been excluded from the body weight graph. These animals tend to have higher body weight and longer survival. I would appreciate your clarification as to the rationale for their exclusion.

Thank you for your consideration.

Seeking clarification on Gα protein catalog numbers (Figs. 3F, 3G, 5E)

I am hoping to replicate the GTPase-Glo assays shown in the figures above, and I would greatly appreciate it if the authors could share the specific Abcam catalog numbers for the recombinant G13, Gi2, Gs, and Gq proteins used.

When I looked for these proteins from Abcam for my own experiments, I learned that only Gs (ab268602) and Gi2 (ab268600) are validated as "Active" using the GTPase-Glo assay—the same assay system used in this study.

For G13, the only available product (ab268597) is explicitly labeled as lacking validated biological activity. When I contacted Abcam directly, I learned that the reason for this is that it is purified using an elution buffer optimized for solubility and recovery efficiency rather than biological activity. Abcam also noted that while some E. coli-expressed proteins retain activity, this is not generally expected under these conditions. A similar caveat applies to wheat germ-expressed proteins, which may lack mammalian-specific chaperones required for proper folding.

Given the seemingly positive GTPase activity reported for G13 in this study—a result that is unexpected given Abcam's guidance that their G13 product (ab268597) lacks validated activity due to harsh elution conditions prioritizing recovery over proper folding—I would be very grateful if the authors could clarify the specific catalog numbers used for G13, Gq, Gi2, and Gs, share information regarding the positive and negative controls (e.g., GDP-bound or GTPγS-bound forms) employed in these assays, and indicate whether, if products not designated as "Active" were used, any specific refolding protocols, buffer exchanges, or GST-tag cleavage steps were employed.

Any methodological details the authors could share would be extremely valuable for replication efforts. Thank you in advance for any information you can provide.

I would like to ask about the consistency of the GTPase-Glo assays in Figs. 3F, 3G, and 5E with a related publication by overlapping authors. The paper below shares two authors with Oda et al., 2021 (Dr. Toyoshima and Dr. Ishihama) and similarly examines interactions between alpha-1-antitrypsin C-terminal peptides and Gα13:

Park Y, Matsumoto S, Ogata K, Ma B, Kanada R, Isaka Y, Arichi N, Liang X, Maki R, Kozasa T, Okuno Y, Ohno H, Ishihama Y, Toyoshima F. Receptor-independent regulation of Gα13 by alpha-1-antitrypsin C-terminal peptides. J Biol Chem. 2025 Feb;301(2):108136. https://www.jbc.org/article/S0021-9258(24)02638-3/fulltext

Notably, Oda et al., 2021 and Park et al., 2025 both employed GTPase-Glo assays but reached opposite conclusions regarding Gα13 activity regulation. I have summarized the specific discrepancies in the figure below.

The Discussion section of Park et al., 2025 citing Oda et al., 2021 attributes the discrepancy to membrane permeability differences between peptides. However, since GTPase-Glo assays are cell-free systems that do not require membrane penetration, shouldn't Park et al., 2025 and Oda et al., 2021 yield identical results? As Dr. Toyoshima or Dr. Ishihama is a shared author on both papers, how do the authors explain these divergent conclusions?

I have an additional question regarding GTPase-Glo assay protocol. Both papers state experiments followed the Promega manual, but I noticed some discrepancies that raise questions about assay validity:

• GTP concentration (10 µM vs. ~5 µM, do not exceed manual announce): Since this kit detects residual GTP via luminescence, substrate excess could undermine quantitative interpretation. Does the 10 µM refer to a 2× stock? If so, what was the final reaction volume, as neither paper specifies this?

• GAP omission in Oda et al., 2021: The manual requires GAP when using GEF buffer—was this omitted based on the assumption that JIP itself acts as both GEF and GAP? Meanwhile, Park et al., 2025 included GAP yet observed no JIP activity, suggesting JIP does not function as a GEF. Given that GAP is necessary to regenerate GDP-bound GTPase for cycle progression, how would a "robust signal" be generated without it?

• DTT concentration (10 mM vs. ~1mM manual recommendation): Could the authors clarify the final concentration, as excess DTT may influence protein folding, peptide–Gα interactions, or the luminescence readout?

I would appreciate clarification on how these conditions align with "according to the manual."

https://www.promega.com/products/cell-signaling/gpcr-signaling/gtpase-glo-assay/

I have several questions regarding the tight junctions (TJs) observed in the cultured A431 cancer cells used in Oda et al., 2021. Could the authors please explain several apparent discrepancies between the text and figures, as well as possible inconsistencies with the cited literature?

Even in untreated subconfluent A431 cells, expression of the TJ component ZO-1 can be observed, although it does not exhibit a sharp belt-like pattern (Fig.6A, Van Itallie et al., 1999). This staining pattern is similar to that observed in JIP-induced tight junctions in Oda et al., 2021 (A431 cells, anti-ZO-1, Fig.S5C), particularly with respect to the presence of strong signals in localized areas.

• Contradiction 1.
  A431 cells treated with the control colon-conditioned medium (CCM) appear to show slight tight-junction formation (Fig.1D). However, the text describes this figure as showing no induction of tight junctions.

• Contradiction 2.
  If Fig. 1D represents a state without tight-junction induction, as stated in the main text, then what kind of state is depicted in Fig. S5B (HBSS), where the signal is completely absent?

• Contradiction 3.
  Oda et al., 2021 states that the cited paper (16, Van Itallie et al., 1995) showed that A431 cells normally do not accumulate tight-junction structures. Actually, in Oda et al., 2021, images lacking detectable signal are presented as supporting evidence (Fig.S5B). However, in the actual cited paper (16), although the localization pattern is described as “more homogeneous” and “nonjunction-like,” expression of ZO-1 (a tight-junction component) is still clearly visible. This interpretation may not fully align with the findings reported in the cited study.

Of particular concern is the fact that Van Itallie et al., 1995 (16) showed that A431 cells appear to develop fairly distinct TJ structures once they reach a confluent state. In Oda et al., 2021, the authors seeded cells at 5 × 10⁴ cells/well in 24-well plates and cultured them for 4 days. Under these conditions, the confluency would presumably reach approximately 80–100%. At such levels of confluency, even slight differences in cell density could influence the apparent presence or absence of tight-junction structures (see 16, Fig.1 and Fig.2b).

Moreover, because JIP is a peptide, its physical and electrical effects on cells cannot be ignored compared with HBSS treatment, which contains no control peptide. Under such influences, it is reasonable to assume that confluency at the time of sampling may differ between conditions even when the culture duration is identical.

Furthermore, the Abcam product page for the Claudin-1 antibody clearly shows Claudin-1 expression in A431 cells. How do the authors reconcile this observation with the statements made in the paper?

• cited as 16, Van Itallie et al., 1995 Christina M. Van Itallie, Maria S. Balda, James Melvin Anderson; Epidermal growth factor induces tyrosine phosphorylation and reorganization of the tight junction protein ZO-1 in A431 cells. J Cell Sci 1 April 1995; 108 (4): 1735–1742. doi: https://doi.org/10.1242/jcs.108.4.1735

• Van Itallie et al., 1999 Van Itallie, C.M., Anderson, J.M. Tight-junction protein ZO-1 isoforms (α+ and α−) show differential extractability and epidermal-growth-factor-induced tyrosine phosphorylation in A431 cells. Protoplasma 206, 211–218 (1999). https://doi.org/10.1007/BF01288206