Peer review of: TNFAIP8 controls murine intestinal stem cell homeostasis and regeneration by regulating (2020)

Reviewers' Comments: 
 
Reviewer #1: 
Remarks to the Author: 
Building off of earlier findings (Honghong et al, J Immunol, 2015), the authors in the current 
manuscript focus on the role of TNFAIP8 in acute injury and show that TNFAIP8-deficient epithelial 
cells are resistant to tissue damage and have regenerative deficits. Mechanistically, loss of TNFAIP8 
results in increased microbiome-driven basal Akt activation and downstream β-catenin activation. 
Although the concept of this study is intriguing, there are some addressable weaknesses in the 
interpretation of some experiments (e.g., organoid cultures and immunostaining evaluation). Also, the 
discrepancy of decreased numbers of fetal-like cells and the increased expression of regenerative stem 
cell markers in Tipe0-/- epithelial cells should also be further investigated. However, the authors 
general contention that increased microbiome-driven basal Akt activation by loss of TNFAIP8 is 
probably an important contributor to the noted phenotype. Overall, the manuscript is well-written and 
the data support the conclusions. Nonetheless, several concerns need to be addressed in order for the 
manuscript to be suitable for publication. 
 
Major points 
1. In Fig 2, we recommend that the authors evaluate the survival of the organoids more carefully. For 
example, in Fig 2D, the authors only show images of one organoid in each group and there seems to 
be no difference between WT and Tipe0-/- organoid images. Lower magnification images would be 
appreciated. Also, in Fig 2E, the authors claim that novel spheroids are established after media 
withdrawal; however, they do not show whether these spheroids arise from established previous 
organoids, which makes it hard to interpret these data. The discussion regarding this observation is a 
bit confusing. 
 
2. On page 8, the authors mention the discrepancy of decreased number of fetal-like cells and 
increased expression of regenerative stem cell markers in Tipe0-/- epithelial cells. From this finding, 
they conclude that a proper regeneration program is not engaged. The authors need to clarify this 
point or investigate this mechanism further. 
 
3. In Fig 5, the author state that loss of Tipe0 results in upregulated Akt signaling in a microbiota-
dependent manner. These conclusions are largely supported by pAkt immunostains in Fig 5D and E. 
However, the background staining for Tipe0-/- mice are much stronger compared to that of WT or 
antibiotic depletion mice (note background staining of muscularis propria in Tipe0-/- intestines), which 
may preclude proper evaluation of any reported difference. Also, in Fig 5C, there is no band for β-
catenin by immunobloting of WT enterocytes, but there is band for β-catenin by immunoblotting for 
WT enterocytes in Fig. 5F—clarification/discussion is needed for these differences. Do commensals 
also regulate β-catenin expression? Perhaps assessing β-catenin in crypts versus villi would be helpful 
as WT crypts should also have robust β-catenin staining. Is the β-catenin accumulation nuclear, 
cytoplasmic or both in vivo? 
 
4. In Fig E5A, TIDE indel analysis shows insertions in the negative control gRNA clone, can the authors 
explain this should be explained. 
 
Minor points 
1. In Fig 3A, alkaline phosphatase staining cannot be recognized in the epithelial cells of both WT and 
Tipe0-/- organoids. 
 
2. In Fig 5A, immunostaining for β-catenin does not show nuclear staining. The authors should 
evaluate the number of cells with nucleus staining. 
 
 
 

Reviewer #2: 
Remarks to the Author: 
Goldsmith and coauthors present a timely study examining the process of intestinal epithelial 
regeneration. Specifically, the authors focused on the role of TNF-alpha induced protein 8-like (TIPE), 
a lipid transport protein that regulates PI3K-mediated signaling. The authors examined the role of 
TIPEO in intestinal injury and show that loss of TIPEO results in resistance to epithelial injury. The 
authors show that TIPE0 is a regulator of intestinal regeneration by functioning to inhibit activation of 
Akt, downstream B-catenin accumulation, and subsequent induction of B-catenin target genes. They 
demonstrate that TIPE0 regulates Akt signaling by extracting PIP2 from the membrane, reducing the 
amount of PIP3 produced and thus inhibiting availability of PIP3 to activate the Akt signaling cascade. 
The authors suggest that this abberant activation of Akt is responsible for inhibition of YAP-driven 
fetal-reprogramming in regeneration, although the link between Akt and YAP was not directly shown. 
 
Overall, this is an interesting study focused on intestinal epithelial regeneration. Much of the proposed 
pathways seem to corroborate previously established links (e.g. ability of TIPE proteins to suppress 
PI3K signalling, etc…), with the exception of TIPE0 removing PIP2 from the membrane which is a 
novel observation. Additionally, the major novelity of this study appears to lie in the findings that TIPE 
knockout mice are resistant to injury in association with a hyperproliferative response that results in a 
lack in epithelial differentiation and a deficiency of regenerative/reserve stem cells, suggesting that 
TIPEO is important in regulating the stem cell niche. 
 
Although, the authors conducted a significant amount of experiments to support most of their 
conclusions, there are some significant shortcomings that make it difficult to accept the manuscript in 
its current form. Some major concerns include: 
 
1) A major problem with the paper is the consistent lack of adequate image quality and resolution 
throughout. Although there is quantification provided, many of the histologic and fluorescent stained 
images are low power images with the stained cells being difficult to see and assess (examples of 
inadequate images include Fig 2L, 3C, 3F, entire Fig4, Fig 5A, etc). This makes interpretation of the 
results impossible and needs to be modified. Inclusion of higher power images, perhaps even including 
arrows to highlight was the reader should be seeing would be very helpful. 
 
2) In the results section, the authors sometimes make definitive statements that seem a bit 
overreaching. For instance, on page 6 when referring to “TipeO-/- enteroids surviving exposure to 
TNFa compared to WT”, as it is currently written, the authors seem to imply that WT organoids don’t 
survive at all while Tipe-/- organoids do. In reviewing Fig 2A and 2B, however, both WT and TipeO-/- 
organoids were susceptible to TNFa or radiation induced toxicity but TipeO-/- organoids have a ~10% 
increase in survival, albeit this is a significant difference. 
3) The authors make the claim that loss of TIPEO results in increased AkT in a microbiome driven 
response. This appears to be a major point in the discussion yet the data provided to make this 
conclusion appears weak. The data provided to support this claim, from what I can tell is simply Figure 
5E and F in which antibiotics resulted in the lack of pAktS473 staining. This observation is weak at 
best. First, there is no positive control for the pAktS473 staining shown in the antibiotic experiment so 
its hard to say if this was simply a technical limitation of the study or truly an absence of pAktS473 
staining (this applies to both 5E and 5F). Second, to make the claim that “TIPEO normally inhibits 
microbiome-induced Akt activation” based on IHC staining and a Western for pAktS473 is not 
sufficient. If this is going to be a major point of the paper, then it would be nice to see other measures 
of Akt activity in antibiotic treated WT and TIPEO mice? Thirdly, is there a difference between the WT 
control in Fig 5B-C and 5E-F? Because it seems that B-catenin is absent in 5C but present and 
detectable in 5F? 
4) Another important point is it would be nice to know what happens to TIPEO expression in WT mice 
during injury? If this is known, then the authors should at least discuss the data, and if not this would 
be nice to include as a rationale to demonstrate its importance in regeneration. 
 

Minor points to address include: 
5) Switching between analysis of mice/enteroids at baseline and during various types of injury (GF 
withdrawal, DSS, irradiation, I/R, etc…) impeded the logical flow of the paper. Could data perhaps be 
rearranged to make the comparison between homeostasis and injury more smooth. Additionally, 
clarification of what growth factor removal does would be helpful. This was not clear from the results 
or Figure Legends. 
 
6) In Figure 1: 
o Authors claim there is no change in cytokine levels but some of the cytokines look very different 
between knockout groups 
o The claim that protection in Tipe0-/- mice is strictly epithelial-dependent is weak as it is ubiquitously 
expressed and although a BMTx experiment was alluded to, this does not prove that it is strictly 
epithelial and perhaps this statement can be soften (i.e. suggests that…) 
 
7) In Figure 2: 
o In Figure 2D, the oganoids look the same in WT and KO organoids across all time-points (i.e. both 
groups look like they are dying) 
♣ How was survival quantified? Methods section suggests that they used CellTitreGlo – data for this? 
♣ Better quality images were significantly improve figure. 
o 2J) Unclear what is being shown with white arrows 
o Unclear why some Tipe0-/- organoids are unable to grow but others are hyperproliferative – seems 
paradoxical and not really addressed 
 
8) In Figure 3: 
o 3F) Would have liked to see quantification of data for #Paneth cells/crypt-villus unit. 
♣ 3G) Hard to interpret data here but would be nice if authors could better describe what they are 
trying to show – i.e. in particular where are the Lgr5+ cells and Fetal-like cells because as it stands, I 
cannot see either population? 
o 3G-H) They claim decreased levels of differentiated lineages in Tipe0-/- mice – however there seems 
to be an increase in EE cells and goblet cells? Does this not go against the claim there are less 
differentiated cells with TipeO-/- mice? 
 
9) In Figure 4: 
o The authors claim that Tipe0-/- mice have inappropriate basal activation of the Sca1+ injury 
response but there is no link to Yap shown. For instance, it would be nice to know if basal Yap is 
upregulated in these mice as well? 
o Unclear explanation of the discretion between fewer Sca1+ cells in Tipe0-/- mice and what seems to 
be activation of the program at baseline 
 
10) In Figure 5: 
o 5A) Overall KO image looks brighter here, not just the green – altered exposure of images 
confounding results? 
o Good link showing loss of Tipe0 upregulates pAkt and downstream B-catenin which are both reduced 
with antibiotic treatment 
o 
11) Extended figures: 
o Data with missing quantification in many of these figures 
 
12) The authors provided data showing that the Wnt antagonist IWP-2 did not block the formation of 
Sca1+ spheroids but IWR-1-endo (promotes B-catenin degradation) abolished all Sca1+ spheroids 
that appeared upon GF withdrawal, indicating that non-Wnt-dependent B-catenin accumulation was 
responsible for development of the Sca1+ spheroids. In this setting, do the authors know what is then 
responsible for B-catenin accumulation if not Wnt? 
 

 
 
Reviewer #3: 
Remarks to the Author: 
Remarks to the Author: 
 
In the current manuscript the authors reported a potential role of TNFAIP8/Tipe0 in inactivating 
PI3K/Akt signaling in IECs. In addition, the authors suggested that in the absence of TNFAIP8/Tipe0 
the enterocytes are more resistant to injury with a hyperproliferative phenotype. Furthermore, the 
authors observed strong defects in the differentiation process in the intestinal epithelium (strong 
induction of Clu+ regenerative program and a marked increase in the expression of Sca1) when 
TNFAIP8/Tipe0 was missing. Furthermore, upon injury TNFAIP8/Tipe0 deficiency resulted in a 
defective epithelial regeneration. 
 
While the topic in principle is interesting unfortunately at the current stage the manuscript lacks 
significantly in quality and structure and appears rather premature. In general, the experimental 
approach is correct and well described but the rationale and the results from those experiments do not 
support the conclusions drawn here. Therefore the data presented here need further strengthening to 
support conclusions made. 
CRITIQUES. 
1. Figure 1. Injury score for healthy KO animals must be shown (Figure 1A). In figure 1B, 
representative images of the intestinal mucosa in healthy KO animals are missing. Incorporating low 
magnification images in figure 1B must be considered. Cytokine expression, secretion and production 
must be evaluated in the intestinal mucosa of healthy KO animals and not only after I/R. The 
expression and localization of Tipe0 and Tipe2 proteins needs to be evaluated in the whole mucosa 
and in freshly isolated crypts of healthy and I/R WT mice (IHC and RT-PCR, could be used). In figure 
E1, proper controls using healthy KO animals are also missing. Quantitation in figure E1D is necessary 
and the analysis for Tipe0 should be incorporated. In figure E1D, the use of specific markers to 
evaluate different immune cell populations present in the intestinal mucosa is highly recommendable. 
The images used in figure E2 are poor quality (Tunel and active caspase 3 staining) should be 
replaced. Quantitation is also required and must be performed in healthy conditions for both, Wt and 
KO animals. Why is some Tunel staining observed in healthy adjacent tissue in figure E2C? Why the 
image presented as WT I/R90 in figure E2B is so different to the figure used as WT I/R90 in panel 1B, 
low magnification images with high magnification insets should be more appropriate to illustrate both 
panels. 
 
2. Important: Authors should consider eliminating experiments carried out with Tipe2 animals. 
 
3. Figure 2. Results in figure 2 are very interesting but difficult to connect. E.g. in the absence of 
Tipe0 IECs are resistant to injury, more proliferative but displayed less intestinal epithelial stem cells 
per unit area. The images presented in Figure 2J are very poor quality. Authors need to clarify if the 
treatment with TNF was carried out overnight (Text) or for 24h (Figure and figure legend). The 
incorporation rate for EdU and BrdU at basal states in WT and Tipe0 KO animals should be evaluated 
and quantitation presented. In figure 2L, the pulse and chase experiments suggest a high rate 
turnover of IECs lacking Tipe0, is apoptosis increased in those animals? Is the crypt length different in 
WT and Tipe0 KO animals? Those parameters must be evaluated and the results incorporated in the 
manuscript. 
 
4. Figure 3 and 4. Is difficult to understand the logical behind the experiments presented in both 
figures. E.g. why the authors analyzed the expression/presence of alkaline phosphatase and keratin 
20 in Wt and Tipe0-/- organoids? Why the authors used DSS induced colitis as a model in figure 4, 
given that DSS mainly affects the colon and the experiments in Figure 1 and 2 are in small intestine. 
Also, a clear connection between the findings reported in figure 3 and 4 and the results reported in 
figure 1 and 2 is missing. In figure 4, the use of Lgr5 reporter mice instead of Lgr5 antibodies is highly 

recommended. IF images in figure 4 must be improved. Figure 3A needs to be improved/replaced. 
 
5. Figure 5 and 6. The results in figure 1 and 2 are clearly linked to the changes induced in Akt 
signaling (figures 5 and 6) by the absence of Tipe0 protein, however the connection stablished with β-
catenin signaling is confusing. TNFAIP8/Tipe0 absence drives Akt hyperactivation but did not affect Erk 
1/2 signaling (Figure 5 and data not shown), the effect of Tipe0 in Erk must be shown.