Inceptor counteracts insulin signalling in β-cells to control glycaemia
Authors: Lena Oppenländer
Chirag Jain
Gustav Collden
Matthias H Tschöp
Michael Sterr
Sarah Homberg
Ansarullah
Fataneh Fathi Far
Aurelia Raducanu
Amir Morshedi
Silvia Schirge
Oliver Plettenburg
Katharina Wißmiller
Julius Wiener
Annette Feuchtinger
Aimée Bastidas-Ponce
Martin Irmler
Ünal Coskun
Regina Feederle
Heiko Lickert
Johannes Beckers
Johanna Siehler
Felizitas Gräfin von Hahn
Michal Grzybek
Matthias Meier
Timo D Müller
Sara Bilekova
Christin Ahlbrecht
Journal: Nature (2021)
Discipline: Multidisciplinary
Keywords: insulin resistance; insulin-like growth factor 1; pancreatic β-cells; inceptor; Iir gene
Affiliations: Institute of Diabetes and Regeneration Research, Helmholtz Center Munich, Neuherberg, Germany., German Center for Diabetes Research (DZD), Neuherberg, Germany., School of Medicine, Technical University of Munich, Munich, Germany., Helmholtz Pioneer Campus, Helmholtz Center Munich, Neuherberg, Germany., Department of Microsystems Engineering (IMTEK), University of Freiburg, Freiburg, Germany., Institute of Diabetes and Obesity, Helmholtz Center Munich, Neuherberg, Germany., Institute of Experimental Genetics, Helmholtz Center Munich, Neuherberg, Germany., Chair of Experimental Genetics, School of Life Sciences Weihenstephan, Technical University of Munich, Freising, Germany., Core Facility Pathology and Tissue Analytics, Helmholtz Center Munich, Neuherberg, Germany., Paul Langerhans Institute Dresden of Helmholtz Center Munich, Dresden University of Technology, Dresden, Germany., Institute for Medicinal Chemistry, Helmholtz Center Munich, Neuherberg, Germany., Institute of Organic Chemistry, Center of Biomolecular Research, Leibniz University Hannover, Hannover, Germany., Monoclonal Antibody Core Facility, Helmholtz Center Munich, Neuherberg, Germany., Institute for Clinical Chemistry and Laboratory Medicine, Faculty of Medicine and University Clinic Carl Gustav Carus, Technical University Dresden, Dresden, Germany., Institute of Diabetes and Regeneration Research, Helmholtz Center Munich, Neuherberg, Germany. ., German Center for Diabetes Research (DZD), Neuherberg, Germany. ., School of Medicine, Technical University of Munich, Munich, Germany. .

Abstract:  Resistance to insulin and insulin-like growth factor 1 (IGF1) in pancreatic β-cells causes overt diabetes in mice; thus, therapies that sensitize β-cells to insulin may protect patients with diabetes against β-cell failure1-3. Here we identify an inhibitor of insulin receptor (INSR) and IGF1 receptor (IGF1R) signalling in mouse β-cells, which we name the insulin inhibitory receptor (inceptor; encoded by the gene Iir). Inceptor contains an extracellular cysteine-rich domain with similarities to INSR and IGF1R4, and a mannose 6-phosphate receptor domain that is also found in the IGF2 receptor (IGF2R)5. Knockout mice that lack inceptor (Iir-/-) exhibit signs of hyperinsulinaemia and hypoglycaemia, and die within a few hours of birth. Molecular and cellular analyses of embryonic and postnatal pancreases from Iir-/- mice showed an increase in the activation of INSR-IGF1R in Iir-/- pancreatic tissue, resulting in an increase in the proliferation and mass of β-cells. Similarly, inducible β-cell-specific Iir-/- knockout in adult mice and in ex vivo islets led to an increase in the activation of INSR-IGF1R and increased proliferation of β-cells, resulting in improved glucose tolerance in vivo. Mechanistically, inceptor interacts with INSR-IGF1R to facilitate clathrin-mediated endocytosis for receptor desensitization. Blocking this physical interaction using monoclonal antibodies against the extracellular domain of inceptor resulted in the retention of inceptor and INSR at the plasma membrane to sustain the activation of INSR-IGF1R in β-cells. Together, our findings show that inceptor shields insulin-producing β-cells from constitutive pathway activation, and identify inceptor as a potential molecular target for INSR-IGF1R sensitization and diabetes therapy. 

Retracted: No

PubPeer comments:
 This is an interesting paper that may deserve a post-publication review. It says that Owing to the similarities between KIAA1324 and INSR, IGF1R and IGF2R in terms of their extracellular domain and KIAA1324u2019s inhibitory function (...), we chose to rename KIAA1324 as the insulin inhibitory receptor, or inceptor (gene name: *IIR* (human) or *Iir* (mouse)) Should we really rename a human gene based on an experiment of a mutant mouse gene? Although the accompanying [press release] even puts the finding in one row with the discovery of insulin by [Banting and Best] the proposed name *inceptor* seems to be a misnomer as it sounds like a new [GO] top hierarchy term like *receptor*. Right now there is no evidence that KIAA1324 is of such an importance. There are numerous reasons why a mutant mouse strain may not represent human biology at all (parent offspring epigenetic effects, embryonal activity, immunology inference, etc.) where up to 90% of results [fail to translate to humans] . I therefore believe that renaming a human gene is not justified (I am even confused with the 2018 patent of H.L. and u00dc.C. renaming it IGFR-l2 and the thesis of F.v.H. renaming it IGFR-L). Second. According to the authors the starting point of the study was a genepaint image (in their [own 2016 study] mRNA 5330417C22RIK wasn t relevant at all). So I assume that the authors refer to image C3753.2.3.C from https: gp3.mpg.de results EIGI121 while the correct reference for that may have been [Dioux-Roux et al.] instead of writing of any own discovery Discovery of inceptor. We identified the 5330417C22Rik mRNA as strongly expressed... While I also see the signal in the pancreas gonad region at the genepaint web gallery, I wonder why the authors omitted the equally strong ( funny) signal in the head region of the same series? ![file] Third. IMHO replication of a conditional knockout, WGS and RNAseq would be helpful to exclude any leaky recombinase expression. **Didn t tamoxifen treatment also bias KIAA1324 (and or IGF1) gene expression?** Tamoxifen elimination half life in humans is approx 7d; receptor affinity of metabolites is high while tamoxifen itself is [pro apoptotic] and may [induce autophagy] itself. Any brief washout period may not be sufficient. ![file] Fourth. The decision to include an outcome in the paper (for example in Fig 1) seems to be based on the significance level as all  non-significant results are buried in the supplement. This strategy may distort the conclusion in particular as measurements are difficult to compare due to variable group size (a flow diagram of all included animals would have helped and is mandatory in clinical research, see [CONSORT](http: www.consort-statement.org consort-statement flow-diagram)). Altogether there are 89 insulin and 34 glucose measurements if I counted it correctly but there are only 16 glucagon measurements. The group difference of glucagon is bigger than the reported insulin and glucose levels but show up only in the supplement. The results are expressed as mean u00b1 s.e.m. or as otherwise specified from at least three independent biological experiments. A value of P 0.05 was considered statistically significant. Fifth. I think we are living in the [u201cpost pu2009 u20090.05 erau201d] . T tests are not [a good choice here] neither is SEM (the Reporting Summary asks for SD). In many instances also exact p values are omitted as only P 0.0001, p 0.05 or p 0.01 is being reported in Fig 1. There seem to be also numerical errors for example the basic HWE calculation where I get in the postnatal group for 66+ +, 102+ -, 11- - an exact Haldane P of 0.000533. P0 results therefore need to be viewed with caution. ![file] I have doubts on any  signficant difference between groups if SEM bars overlap. ![file] How can different intensities at Western blots turn into identical values after quantification? ![file] Are we dealing here with an u237a or u03b2 cell effect? I don t know as the authors switched outcome here. Numbers are too low for any meaningful conclusion. ![file] Sixth. There are also inconsistencies in labelling the animals and loading controls when comparing the data presented here with the [thesis of F.v.H.] . ![file] There is another inconsistency in labelling animals 36D7 and 31A11. ![file] Seventh. Moving now to content, I wonder why a seminal paper by [Deng et al.](doi:10.1038 cddis.2010.9) (who discovered KIAA1324) is not being cited here **although Lei Deng explained KIAA1324 related autophagy 10 years earlier**. Subcellular fractionation and immunofluroscent labeling indicated that EIG121 was a transmembrane protein localized in the plasma membrane-late endosomeu2013lysosome compartments. ... In cells overexpressing EIG121, cytoplasmic vacuoles accumulated after EIG121 induction, and the autophagosome marker LC3 translocated into punctuate, dot-like structures. Electron microscopy revealed that in cells overexpressing EIG121, autophagosomes were markedly increased. ... When combined with starvation or cytotoxic agents, EIG121 knockdown greatly increased apoptosis. Our results suggest that EIG121 is associated with the endosomeu2013lysosome compartments and may have an important role in autophagy. KIAA1324 was found in a RNAseq screen of u00df cell autophagosome formation ([Cnob et al.] ) while also [Estrella 2014] showed that KIAA1324 is an expressed pancreas gene. All these references have been known to the authors as they have been [thesis] advisers of F.v.H. She reports on p36 even another papers that is omitted here EIG121 was shown to play a role in the autophagy-related maintenance of cancer stem cell homeostasis [Ran, Zhou, Zhang, 2017] . So numerous key facts had been known. Nevertheless the 2018 patent of the authors reads in paragraph 0013 However, nothing was known, let alone speculated about a role of KIAA1324 or KIAA1324L in metabolism, let alone cancer. This role was for the first time attributed to said proteins by the present inventors. Eighth. Some questions raised here or in the accompanying [editorial] maybe already answered by the previous literature. [GWAS] in humans never found a major diabetes or cancer hit on KIAA1324 while also [ClinVar] has only a few isolated entries, most of them being benign. A KIAA1324 49kB deletion described by [Jaillard 2016] resulted in secondary amenorrhoea and high FSH levels but not diabetes. Ninth. While I cannot exclude any specific effect of any potential antibody or a small organic compound, common knowledge argues against therapeutic use. KIAA1324 expression (also known as Estrogen-Induced Gene 121, EIGI121) may be lower after menopause (where insulin resistance and T2D increases). We may assume that also from an earlier Cell paper where KIAA1324 expression in the pancreas turned out to [be age dependent] 31053-X) (table S3, line 100). Maybe the authors missed also the clinical fact that there is a reduction in glucose levels among postmenopausal women [who use estrogen therapy] . So women may have already suppressed KIAA1324 unwittingly. Tenth. Does  supervising of study or  generating antibody (no study planning otherwise, no experiment, no analysis, no writing) qualify for authorship? At least [COPE] guidelines do nor recommend that. 6 authors sharing first authorship seems to be a new record. Unfortunately most of them are not identified by their ORCID ID, so Ansarullah is otherwise just an [alias of a religious organization] ). Maybe the authors could comment on that? , 
 #1 I can help with the overlapping SEMs reported as significant. The authors analysed a repeated-measures design with a two-way ANOVA. The latter assumes that the data at each time point are independent of the others, i.e. that they come from different animals; they don t. Analysed correctly, the difference at the peak might *just* be significant at p 0.05 in a direct test, but that probably wouldn t survive any correction for multiple comparisons. The ANOVA is also invalid for a second reason: *heteroscedasticity* or unequal variances. The pooled variance employed in the post-hoc test will have been artificially depressed by the points with little to no variability at 0 and 120 minutes. ![image] , 
 #1 RE Fig 2 j-k: * How can different intensities at Western blots turn into identical values after quantification? * It is self-evident that the intensities were normalized to the first condition (= 1.0) independently for each of the three replicate sets (n = 1, 2, 3). How can that possibly be difficult to understand? (Update edit: Note that it is clear from blots provided in the source data that the 12 samples were not all on the same blot; generally, the samples from n = 1 and 2 were on one blot, and those from n = 3 on a separate blot. Hence, the absolute intensities between different blots cannot be compared directly, but they can be normalized to the first condition for each set.) , 
 * RE: #1: * I have doubts on any  signficant difference between groups if SEM bars overlap. * * RE: #2: * Analysed correctly, the difference at the peak might just be significant at p 0.05 in a direct test, but that probably wouldn t survive any correction for multiple comparisons. * Both #1 and #2 are expressing doubts apparently based on gut instinct without any reference to the actual source data that are published with the paper. As an exercise, if we check #2 s claim about a  direct test , prior to multiple comparison correction, a t-test on the posted data yields the following. It refutes the gut instinct of #1, as well as #2 s suggestion that the differences might only  just barely be p 0.05 (note -- it s unclear to me if #2 regarded the  peak as 15 min [CKO] or 30 min [control]): ![file] It is easy to be a critic, but harder to be constructive. If #2 purports to know a better statistical test to use here, go ahead and apply it to the posted data and see if it changes the interpretation. Otherwise this is a lot of fuss over a nit-picky point. While we wait for #2 to provide the correct test, we can apply some common sense. Namely, multiple comparison correction is necessary to avoid being fooled by cherry picking one pair-wise comparison out of many. But here, all three non-baseline comparisons (15, 30, 60 min) are significantly different. So there is not a cherry picking problem here, and the interpretation is unlikely to be changed by a multiple comparison correction. The authors used Bonferroni, but choose your preferred method and tell us if anything changes. Finally, I did notice that the number of measurements in the posted source data does not match that listed in the Figure legend. The legend states  control (n = 12) and CKO (n = 15) , but the source data suggest n = 10 and 13, respectively. So, there is an error in one or the other that should be addressed. , 
 #4 Previous #2 here (although that can t be proven). You are correct, Leucanella. Thank you for catching my error. I apologise to the authors. My misapprehension was caused by the fact that the authors appear not to have plotted the SEM, but something broader - presumably the SD. The eyeballing would have been correct if they had been SEMs (the means should in fact be even further apart than non-overlapping SEMs). In my defence, I *did* check the legend before posting; it says:  Data are mean u00b1 s.e.m. (bu2013g, i, k, m, n). , 
 #5 Indeed, the published source data for Fig 2d confirms your suspicion that the error bars show the SD rather than the SEM. Here is what I calculated from the datapoints provided; you ll see that the plotted error bars match the SD values, not the SEM values: ![file] ,