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Response to comment on 'AIRE-deficient patients harbor unique high-affinity disease-ameliorating autoantibodies'

  1. Christina Hertel
  2. Dmytro Fishman
  3. Anna Lorenc
  4. Annamari Ranki
  5. Kai Krohn
  6. Pärt Peterson
  7. Kai Kisand  Is a corresponding author
  8. Adrian Hayday  Is a corresponding author
  1. ImmunoQure AG, Germany
  2. University of Tartu, Estonia
  3. King’s College London, United Kingdom
  4. University of Helsinki, Finland
  5. Francis Crick Institute, United Kingdom
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Cite this article as: eLife 2019;8:e45826 doi: 10.7554/eLife.45826

Abstract

In 2016, we reported four substantial observations of APECED/APS1 patients, who are deficient in AIRE, a major regulator of central T cell tolerance (Meyer et al., 2016). Two of those observations have been challenged. Specifically, ‘private’ autoantibody reactivities shared by only a few patients but collectively targeting >1000 autoantigens have been attributed to false positives (Landegren, 2019). While acknowledging this risk, our study-design included follow-up validation, permitting us to adopt statistical approaches to also limit false negatives. Importantly, many such private specificities have now been validated by multiple, independent means including the autoantibodies’ molecular cloning and expression. Second, a significant correlation of antibody-mediated IFNα neutralization with an absence of disease in patients highly disposed to Type I diabetes has been challenged because of a claimed failure to replicate our findings (Landegren, 2019). However, flaws in design and implementation invalidate this challenge. Thus, our results present robust, insightful, independently validated depictions of APECED/APS1, that have spawned productive follow-up studies.

https://doi.org/10.7554/eLife.45826.001

Introduction

In 2016, in a paper published in Cell, we made at least four substantial observations concerning APECED/APS1 syndrome patients who are defined by deficiency in the AIRE gene, a major regulator of central T cell tolerance: i) that such patients share autoantibodies to a small subset of proteins, including Type I IFNs, Interleukin-(IL)−17, and IL-22, that was previously reported (Kisand et al., 2010; Meager et al., 2006); ii) that, quite surprisingly, many such naturally-arising antibodies are conformation-specific and of extremely high affinity, potentially explaining their powerful neutralizing capacity; iii) that most APECED/APS1 patients additionally harbor ‘private reactivates’ collectively targeting very many autoantigens; and iv) that strong antibody-mediated neutralization of IFNα correlated significantly with an absence of Type I diabetes (T1D) in patients otherwise highly disposed to it (Meyer et al., 2016). These observations formed the basis for several substantial follow-up papers in peer-reviewed journals (Rodero et al., 2017a; Frémond et al., 2017; Fishman et al., 2017).

Our 2016 paper discussed the close alignment of our first substantial observation with contemporaneous work by Landegren and co-workers that likewise featured a protein microarray screen of patient versus control sera (Landegren et al., 2016). Our second substantial observation could not be compared because Landegren and co-workers did not investigate the properties of the autoantibodies that were identified. Nonetheless, Landegren and other co-workers now dispute our remaining two claims (Landegren et al., 2019). While we welcome open, constructive discourse about science, we are disappointed by this dispute because we believe it reflects simple but important differences between our approaches that could have been easily resolved, had Landegren and co-workers approached us directly. Those important differences are explained below. Based on biological significance, they are considered in reverse order to their consideration in Landegren et al. (2019) (hereafter referred to as the comment).

Results and conclusions

No association between neutralizing autoantibodies to interferons and Type 1 diabetes in APECED/APS1

The comment disputes our observed correlation of strongly neutralizing IFNα autoantibodies with reduced incidence of T1D, claiming to have essentially repeated our experiment, but finding no difference in the IFN neutralization capacity of sera from APECED/APS1 patients with or without T1D.

In fact, the comparison that is described in the comment of IFN neutralization in two APECED/APS1 patient cohorts defined simply as with or without diabetes did not repeat our experiment. We did not claim that differential Type I IFN neutralization is the sole regulator of T1D incidence. Rather, we hypothesized that the significance of differential Type I IFN neutralization might relate to the differential disease development in patients uniformly displaying pathognomonic features of T1D. Thus, we compared IFNα neutralization in two patient sub-cohorts: one presenting with T1D and one not, but all of whom either harbored and/or had harbored disease-associated, anti-islet antibodies, for example anti-GAD65, anti-GAD67, that are widely-utilized clinical indicators of T1D-risk. Supporting our hypothesis, we observed a statistically significant correlation of low neutralization and T1D, consistent with several other experiments in which we established the capacity of APECED/APS1 autoantibodies to ameliorate immunopathology.

It is also unfortunate that an imperfect study design was employed in the comment. As presented to us, the comparison of different sera in the comment was made at a single [high] concentration (10%), which is inappropriate because it will most often saturate the assay, thereby failing to appropriately discriminate low versus high neutralizing activities. To illustrate this point, we re-examined IFNα neutralization, using a dose-dependent, cell-based assay that measures IFN-stimulated release of alkaline phosphatase (AP), as we previously described (Meyer et al., 2016), but mimicked the comment in examining only the effects of 10-fold diluted sera. This masked any significant differences between GADA-seropositive patients with or without T1D (Figure 1A). By contrast, when sera were serially diluted so as to imbue the assay with appropriate sensitivity (as described in the Meyer et al., 2016), the patients’ broad dynamic range of IC50 values was revealed, with clear segregation of the patients with and without T1D (Figure 1B and C). Indeed, among 13 patients without T1D, the serum of only one (‘N’; Figure 1C) showed low IFNα neutralization, comparable to that of all the patients with T1D.

The comparison of two different strategies to measure IFNα neutralizing capacity of APECED/APS1 serum samples.

In panel (A), the same reporter cell assay (HEK-Blue IFN-α/β cells from InvivoGen) has been applied as in Meyer et al. (2016) but at a single high serum concentration (ns: not significant). (B) Representative fitted dose-response curves that were used in Meyer et al. (2016) to calculate IC50 values for each serum sample. Individual curves are represented with dotted lines and those for grouped values in solid lines (mean ± SEM). (C) IC50 values (expressed as the dilution of serum sufficient to neutralize 50% of IFNα2 activity [12.5 U/ml]) that were calculated from individual and grouped curves shown in panel B. APECED/APS1 patients with Type 1 diabetes (T1D) are depicted in red and APECED/APS1 patients with GAD65 autoantibodies (GADA) but without T1D are in blue. (D) Neutralization of IFNα2 activity (10 000 U/ml) required to induce pSTAT1 was tested with different dilutions of sera from GAD seropositive patients with and without T1D. 2-way ANOVA was used to calculate P-values [ns – not significant, **p≤0.01, ***p≤0.001, ****p≤0.0001].

https://doi.org/10.7554/eLife.45826.002

The authors of the comment employed a phospho-STAT1 induction assay (Gupta et al., 2016). This is an inherently less sensitive assay, but nonetheless when we adopted it in another new experiment, we obtained the same pattern of results as we obtained with the AP assay. Namely, at high concentrations, the sera of patients with and without T1D showed comparable activities, but at lower, sub-saturation concentrations [50-fold dilutions], the cohort without T1D showed significantly greater capacity to limit IFNα activity (Figure 1D). Thus, because their measurements were insufficiently sensitive to discriminate low neutralizers from high neutralizers, we believe that the experimental design employed in the comment was not appropriate to compare IFN neutralization by the sera of patients with and without T1D: as such, the comment provides no experimental basis on which to dispute the fourth substantial observation of Meyer et al. (2016).

Finally, the observations of Meyer et al. (2016) are germane to an important clinical issue. Specifically, the delayed onset and relatively rare incidence (~15%) of T1D in APECED/APS1 patients is puzzling given that: insulin is a prototypic AIRE-regulated tissue-specific autoantigen; there is defective negative selection of β-cell antigen-specific T cells; pancreatic β-cells are notoriously vulnerable to autoimmune attack; and idiopathic T1D commonly occurs in children and adolescents (Perheentupa, 2006; Anderson et al., 2002; Wolff et al., 2014; Sabater et al., 2005). In this context, the observations of Meyer et al. (2016) suggest that IFN-neutralizing antibodies may delay T1D onset in APECED/APS1 patients and may prevent it completely in those with very high neutralizing titres. This is consistent with longitudinal assessment, albeit limited, reported by in Supplementary Figure 7 of Meyer et al. (2016). When combined with increasing numbers of studies implicating Type I IFN as pathogenic in patients at genetic risk to develop T1D (Ferreira et al., 2014; Kallionpää et al., 2014; Foulis et al., 1987), our data compel us to disagree with the assertion made in the comment that there is insufficient evidence to "embark on in-depth investigations of targeting Type 1 IFNs for the treatment or prevention of Type 1 diabetes."

No evidence for widespread autoantibody reactivity in APECED/APS1 patients

The comment disputes our observations that individual APECED/APS1 patients harbor small numbers of ‘private’ specificities shared by few other patients, but collectively comprising a very large number of proteins.

In fact, our observations conspicuously mirror a key clinical aspect of APECED/APS1, namely that each patient is highly individual in the type and range of symptoms; the rate and course of disease progression; and, to some extent, the time-of-onset. Hence, it makes biological sense that individual patients would harbor correspondingly diverse antibodies as causes and/or biomarkers of discrete clinical courses.

Nonetheless, the comment argues that the private specificities comprise stochastic, irreproducible signals reflecting the high risk of false positives inherent in the statistical methods that we employed to analyse our ProtoArray data.

Importantly, all statistical approaches need to reflect a study’s goals. For example, clinical trials use one type of statistical method to minimize type one errors (false positives) that might misleadingly indicate drug efficacy, while employing different statistical methods to minimize type two errors (false negatives) that might obscure adverse event(s). The approach advocated in the comment (and in Landegren et al., 2016) parallels the former, scoring signals in patients by comparison to mean and standard deviation (SD) of controls, and then additionally adding a Fisher’s exact test to exclude signals that did not confer statistical difference to the whole patient group. This is well-suited to defining how APECED/APS1 patients differ as a group from healthy controls.

By contrast, Meyer et al. (2016) sought to characterize the nature of auto-reactivities in APECED/APS1 patients, including private reactivities that might mirror individual clinical presentations. The Fisher’s exact test filter would exclude ‘private targets’ as outliers or false positives because they are insufficiently frequent to significantly influence the distribution of reactivities across the whole group (see below). Anticipating this, and knowing that no existing standard data-analysis method can unequivocally discriminate private specificities from false positives, we compared the signal to mean and SD of controls without the additional filter (Meyer et al., 2016).

Although, this is a standard, widely-used approach, we do not dispute that it can be confounded by unwarranted assumptions about the behavior of the control cohorts, coupled with an imbalance in the numbers of controls (21) and patients (81) that we examined (Meyer et al., 2016). Hence, false positives can and will arise. Nonetheless, we consciously employed this approach because the validation of real reactivities versus false positives was to be made by a spectrum of additional, independent, serological, biochemical, and biological methods that were employed in Meyer et al. (2016) and subsequently in Frémond et al. (2017). By contrast, in the comment (and in Landegren et al., 2016) the authors went little beyond the ProtoArray, necessitating their adoption of a more conservative statistical approach.

Examples of validation are as follows. First, several private anti-cytokine reactivities were validated by ELISA and by LIPS (Luciferase Immunoprecipitation – an unrelated assay platform using independent sources of target proteins displayed in native conformation), and have since been validated independently (Meyer et al., 2016; Fishman et al., 2017; Sng et al., 2019). Furthermore, we molecularly cloned and fully characterized such autoantibodies, for example anti-IL32γ (Meyer et al., 2016), anti-BAFF (unpublished data), and anti-IL20 (Meyer et al., 2016) detected in five, four, and two patients, respectively, but in none of the sampled controls.

Second, LIPS likewise validated many non-cytokine targets, including but not limited to 24 of 31 testis- and cancer-associated antigens so far tested (Table 1), commonly with good correlation with the ProtoArray signal intensities (Fishman et al., 2017). Those validated targets included twelve testis-specific and CT-antigens (PDILT, MAGE-B2, SPANXD, SPAG8, SPAG16, CT45A3, GAGE1, GAGE7B, MAGE-B1, MAGE-A3, MAGE-4 and MAGE-A10) (Fishman et al., 2017). This overtly contrasts with the comment and with Landegren et al. (2016) in which the ProtoArray analysis identified reactivity to only two CT-antigens (PDILT and MAGE-B2), providing experimental evidence that their statistical methods were too conservative to detect patients’ private reactivities.

Table 1
Testis- and cancer- associated non-cytokine targets screened by LIPS.
https://doi.org/10.7554/eLife.45826.004
TargetLIPS result
SPAG8pos
SPANXDpos
TEX264pos
CT45A3pos
GAPDHSpos
SPAG16pos
PDILTpos
GAGE1pos
SPATA7pos
GAGE7pos
CAPNS1pos
KCNIP2pos
POMZP3pos
MAGEA4pos
RPL12pos
MKNK2pos
S100A7Apos
MAGEA3pos
MAGEB1pos
MAGEB2pos
MAGEA10pos
LCN1pos
FGF12pos
HMGB1pos
TSPY2neg
MORN2neg
CRYGDneg
GNG4neg
RSU1neg
PAGE1neg
PAGE2neg

Third, Fishman et al. (2017) applied very stringent criteria to the data of Meyer et al. (2016), including a further filtration of private reactivities into those shared by >3 patients. Still there were ~1000 reactivities: 490 shared by only three patients; 245 shared by 4 but not five patients; 111 shared by 5 but not six patients; 116 shared by >6 patients. These reactivities individually and collectively displayed five conspicuous traits: (1) correlations with clinical phenotypes, for example pernicious anemia or vitiligo; (2) more reactivities in patients with more complex clinical phenotypes; (3) a correlation of the average number of reactivities per patient with the severity of the AIRE gene mutation; (4) reactivities assessed longitudinally over relatively short time-frames correlated more closely than those sampled over longer time-frames (e.g. 10 years); and (5) reactivities mostly increased with duration of disease (Fishman et al., 2017).

Fourth, the reactivities described by Meyer et al. (2016) were conspicuously enriched in gene-products of two sub-classes: a) those expressed in lymphoid tissues and with no known connection to AIRE function, but which comprise some of the strongest reactivities (as agreed by Landegren et al., 2016 and the comment); b) diverse tissue-restricted antigens (TRAs), which were strikingly enriched in those expressed by AIRE-expressing medullary thymic epithelial cells (Fishman et al., 2017). Consistent with this, male antigens were also targeted in females (Fishman et al., 2017), whereas non-CT-antigen members of the MAGE family that are expressed in all tissues were not observed as targets (Meyer et al., 2016; Fishman et al., 2017).

False positives could not meet any of these four sets of criteria, let alone all of them. In sum, the potential for a signal to be a false positive does not establish that it is, particularly when its validity is attested to by multiple independent means. The comment ignores another pitfall of ProtoArrays, which is the under-estimation of reactivities to proteins that are not displayed well, as we and others have noted (Kärner et al., 2016; Schnack et al., 2008). Critically, ProtoArrays should serve as guides for subsequent experiments, as was the case for Meyer et al. (2016) and a number of later studies (Rodero et al., 2017b; Frémond et al., 2017; Fishman et al., 2017).

In this regard, we note that a co-author of the comment recently published a study (Sng et al., 2019) describing a loss of B cell tolerance in APECED patients that was associated with a broad spectrum of autoantigen reactivities, including several new non-cytoline specificities. This aligns with the depiction of APECED/APS1 patients provided by Meyer et al. (2016).

Conceding, nonetheless, that we may have exaggerated some patient reactivities, we applied a more conservative statistical approach to Meyer et al. (2016): namely we based z-scores on the mean of the controls and SD across all patients plus controls. SD will now be increased by positive reactivities in controls and/or patients, thereby reducing the risk of false positives. Interestingly, this approach identified reactivities overlapping 81% with our original study: again, these comprised broadly shared autoantigens and from ~30 to~100 private specificities that collectively composed a substantial fraction of the proteome. Moreover, when this same statistical approach was applied to an additional study in which we used an earlier version of the ProtoArray (v5.0) to interrogate sera from 23 patients examined by Meyer et al. (2016) but with eight different healthy controls, the overlap across the two independent studies (and platforms) was substantial and highly significant (p<1e-06), far exceeding any overlap obtained from 100,000 random permutations of patients and controls.

We conclude that our published and ongoing studies (Meyer et al., 2016; Fishman et al., 2017) accurately depict the serological status of APECED/APS1 patients, viewed collectively and individually. While we acknowledge that the limited numbers of patients and appropriate controls make it difficult to reach a precise estimate of the numbers of private specificities, there is no basis for disputing the four central findings of Meyer et al. (2016), consistent with which those findings have formed a basis for rigorous follow-up work by us and by others (Rodero et al., 2017a; Frémond et al., 2017; Fishman et al., 2017; Sng et al., 2019; Rice et al., 2018; Llibre et al., 2018; Dhir et al., 2018; Rodero et al., 2017b) that will inform our understanding of APECED/APS1 and of autoimmune diseases more generally.

Materials and methods

Key resources table
Reagent type or resourceDesignationSourceIdentifiers
Cell lineHuman HEK293 cells - Type I IFNs reporter cellsInvioGencat # hkb-ifnab
AntibodyAlexa Fluor 647 conjugated anti-STAT1 (pY701), mouse IgG2aBD Biosciencescat # 562070
Recombinant proteinrecombinant human IFNα2aMiltenyi Biotechcat # 130-093-873

Reporter cell assay

Request a detailed protocol

The IC50 values of IFNα neutralization of serum samples were tested with the help of HEK-BlueTM IFN-α/β reporter cells (InvivoGen) that express alkaline phosphatase (AP) under the inducible ISG54 promoter after ISGF binding to the IFN-stimulated response elements in the promoter. The cells were grown in DMEM supplemented with heat inactivated 10% FBS and 30 g/ml blasticidin (InvivoGen) and 100 g/ml Zeocin (InvivoGen). Cells were stimulated with IFNα2a (12.5 U/ml, Miltenyi Biotech) that was preincubated for 2 hr with serial dilutions of recombinant antibodies or one fixed concentration (10%) of serum. QUANTI-Blue TM (InvivoGen) colorimetric enzyme assay was used to determine AP in the cell culture supernatants after 21 hr of incubation. OD was measured at 620 nm with Multiscan MCC/340 (Labsystems) ELISA reader and IC50 values were calculated from the dose-response curves using GraphPad Prism eight software.

Phospho-STAT1 assay

Request a detailed protocol

Peripheral blood mononuclear cells (PBMC) from a healthy control were isolated with density gradient centrifugation and aliquoted by 500 000 cells to test tubes containing IFN-α2a (10 000 U/ml) pre-incubated with serum dilutions for 2 hr. Tubes with or without IFN alone served as positive and negative controls. After 15 min of stimulation of PBMCs at 37°C, the cells were fixed immediately with Cytofix buffer, permeabilized with Perm Buffer III and stained with PE-conjugated antibody to phospho-STAT1 (Y701; all from BD Biosciences). Data were acquired with LSRFortessa (BD Biosciences) and analyzed with FCS Express (De Novo Software).

References

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Decision letter

  1. Detlef Weigel
    Senior and Reviewing Editor; Max Planck Institute for Developmental Biology, Germany
  2. Christopher C Goodnow
    Reviewer; Garvan Institute, Australia

In the interests of transparency, eLife includes the editorial decision letter and accompanying author responses. A lightly edited version of the letter sent to the authors after peer review is shown, indicating the most substantive concerns; minor comments are not usually included.

Thank you for submitting your article "Response to Comment on 'AIRE-deficient patients harbor unique high-affinity disease-ameliorating autoantibodies'" to eLife for consideration as Scientific Correspondence. Your article, and the original comment by Landegren and colleagues, have been reviewed by two peer reviewers (who have opted to remain anonymous), and the evaluation has been overseen by a Deputy Editor (Detlef Weigel) and the eLife Features Editor (Peter Rodgers).

I am pleased to be able to tell you that we have decided to accept for publication both the original comment and your response to it. The substantive comments in this decision letter will also be published as part of your article (and likewise for the comment from Landegren): you will be able to check these comments when you check the proof of your article.

You will need to make the following changes to your article:

[... ]

Note: The editor handling this manuscript asked the reviewers to answer a number of questions: these questions are shown below in italics; the comments from the reviewers are shown in Roman.

Reviewer #1:

Is the Formal Response substantial enough to merit formal publication? Do you have any substantive concerns about the Formal Response? Do you think that the authors of the original publication should be asked to publish a correction to their work?

The Formal Response addresses the main challenges by Landegren et al. The response correctly points out that there were four major findings of the Cell 2016 paper and that Landegren challenges two of these. I acknowledge that the Cell 2016 paper was a landmark paper of recent years and that the cytokine antibody findings that were validated with LIPS assays in that paper were very impressive.

The formal response by Hertel et al is appropriate in its criticism of one point of contention - the issue of type 1 IFN neutralizing autoantibodies and diabetes development. As mentioned above and in the response, Landegren have reached saturation in their type 1 IFN neutralizing autoantibody assay and, therefore, cannot make their conclusion that there are no differences in type 1 IFN neutralizing autoantibodies between the APECED patients with and without diabetes. The formal response and new data convincingly demonstrate the original claim by Meyer. One point to note, however, is that the majority of GAD antibody positive individuals (healthy or diseased) do not develop Type 1 diabetes (unless they have other Type 1 diabetes autoantibodies) and it is highly unlikely that many of these have high titers of type 1 IFN neutralizing autoantibodies - be careful about over-generalizing the findings from the APECED patients.

The second point of contention is less well defended. Indeed, one expects that many readers of the Cell paper would see the flaws in using Z scores with 21 control samples. This simply cannot be defended. The formal response argues that if they calculated Z scores using all data (patients and controls) they have similar findings, but still there are too few to be conclusive and the imbalance of controls and patients is not overcome by this analysis. The formal response correctly states and appropriately points out that the alternative approach to a threshold will miss private specificities and that they purposefully chose their analysis method to be able to address their question of how broad is the spectrum of autoreactivity in APECED patients. However, they would have needed to include hundreds (at least) of controls to do this.

The second problem is that the disease is rare and, therefore, one must consider private specificities (those seen in occasional patients) as suggestive, but not conclusive. The formal response uses the subsequent paper of Fishman as evidence to support their claims for many of the antigens of their screen. Unfortunately, on their second point of evidence, the Fishman paper shows correlations between the array and the LIPS assay Z scores (note that the LIPS Z scores are actually not very high), which is not entirely convincing as a validation of these antigens and there were only 20 controls. Thus, the formal response is subject to the same flaws - too few controls for Z scores in what they use as evidence to their original claim. Also, I have concerns about Table 1 in the formal response as I don't find the data it is derived from sufficiently conclusive. The formal response argues that they have other sets of evidence that support their claim of broad reactivity, namely their impressive validation of the cytokine autoantibodies in the original paper (and by Landegren), the tissue enrichment of their targets and the association of specificities to disease phenotype, and the more stringent filtering of data in the Fishman paper. These arguments are reasonable.

I do not believe that the authors of the original work should publish a correction, but I do believe that in their response they should have recognized the flaw in defining positivity with Z scores derived from 21 controls and that they should have stated even more clearly that their method of analysis is biased towards identifying false-positives. I believe that it would be fair and objective to say validation was performed for many of the cytokine targets in the original paper and only partially done for some of the other specificities in the Fishman paper. I also suggest that they should have been a little less aggressive in their response.

Specific questions for the original paper (Meyer et al. 2016 Cell 166:582–595) are:

Was the initial screen indeed sufficient to generate a list of candidates that were more likely than expected by chance to show an effect in the experimental follow-up studies?

The initial screen successfully identified and validated a number of cytokines as autoantigen targets. Thus, it was able to show that the screen was sufficient to give rise to a very important and repeatedly validated finding. However, it was inadequate to make the claim that thousands of antigens can be targeted in these patients. The ProtoArray is just not ideal for such a conclusion without testing all the antigens in a different system. It is also way too expensive to be used with hundreds (a minimum) of controls necessary to appropriately define Z scores, and APECED patients are simply too rare to have a sufficiently large cohort to be conclusive about low frequency positive targets. The follow-up studies that did test some of the antigens by LIPS don't do a lot to dampen these limitations since they also don't have many controls and patients.

Are the experimental follow-up studies believable?

The experimental follow-up studies on the cytokine antibodies (the major findings) are entirely credible with validation by ELISA and LIPS, cloning of IgG from memory B cells, neutralizing antibody assays, and subsequent validation by others. The follow-up studies for other antigens reported by Fishman are much less credible.

In rebuttal, the authors of the Cell paper claim that a sampling of the thousands of private specificities were validated. There was no evidence for this in the published study, and unconvincing preliminary evidence here.

Reviewer #2:

Is the Formal Response substantial enough to merit formal publication? Do you have any substantive concerns about the Formal Response? Do you think that the authors of the original publication should be asked to publish a correction to their work?

i) Is the Formal Response substantial enough to merit formal publication?

Yes.

ii) Do you have any substantive concerns about the Formal Response?

No.

iii) Do you think that the authors of the original publication need to publish a correction to their work?

Yes.

Please note that Reviewer #2 made the following comments about your response in their report about the submission from Landegren et al.

- Do you have any substantive concerns about the elements of the article [by Landegren et al.] that challenges the findings of the original publication?

No, the analysis performed by Landegren provide compelling evidence that the original publication in Cell employed a flawed normalization of the analysis of antibody binding to protein microarrays. As a result, the main conclusion in the Cell paper about the much wider breakdown of tolerance in AIRE deficiency, with antibodies recognizing private specificities unique to one or two patients, is erroneous.

In rebuttal, the authors of the Cell paper claim that a sampling of the thousands of private specificities were validated. There was no evidence for this in the published study, and unconvincing preliminary evidence here.

- Are the other elements of challenge [by Landegren et al.] significant enough to merit publication in eLife?

Yes. The second main novel conclusion of the Cell paper was that neutralizing antibodies to interferon were absent from the sera of AIRE deficient patients with Type 1 diabetes compared to those without. Here, studying a larger cohort, Landegren et al find neutralizing antibodies in AIRE deficient patients with or without Type 1 Diabetes. It is possible this reflects differences in assay methodology, but both methods appear equally valid and unlikely to explain the different results.

In rebuttal, the original authors point out that the data in the Cell paper were from serum titrations, and that if they repeat the experiments with serum diluted 1/10 they also now find neutralizing antibodies in both groups. In the Cell paper, the mean IC50 of neutralizing antibodies in patients without Type 1 diabetes was on the order of 1/100,000, at which point there was a difference in titre. However in the data in the rebuttal, the difference in inhibitory activity is only apparent at one dilution (1/50) and not at 1/250 or 1/10. Since the rebuttal now also shows neutralizing antibodies are present in Type 1 diabetes patients at relatively small differences in titre, and since serum is undiluted in vivo, this appears to warrant a revision to the original conclusions in Cell that "those with T1D showed only low or negligible neutralization."

It is nevertheless difficult to extrapolate serum neutralization from in vitro to in vivo, so it would be important for Landegren et al to test interferon alpha neutralization at different serum dilutions to determine if there is a difference in titre in their cohort.

https://doi.org/10.7554/eLife.45826.010

Author response

[This document contains the response from Hertel et al. to specific points in the decision letter sent on 9 April 2019; the full decision letter is available at the following URL: https://elifesciences.org/articles/45826#SA1]

We repeat the reviewers’ points here in italic, and include our replies point by point in Roman.

Reviewer #1:

The formal response by Hertel et al is appropriate in its criticism of one point of contention - the issue of type 1 IFN neutralizing autoantibodies and diabetes development. As mentioned above and in the response, Landegren have reached saturation in their type 1 IFN neutralizing autoantibody assay and, therefore, cannot make their conclusion that there are no differences in type 1 IFN neutralizing autoantibodies between the APECED patients with and without diabetes. The formal response and new data convincingly demonstrate the original claim by Meyer. One point to note, however, is that the majority of GAD antibody positive individuals (healthy or diseased) do not develop type 1 diabetes (unless they have other type 1 diabetes autoantibodies) and it is highly unlikely that many of these have high titers of type 1 IFN neutralizing autoantibodies - be careful about over-generalizing the findings from the APECED patients.

REPLY: We agree with the reviewer, and make clear in our response that neither we nor anyone has suggested that natural Type I IFN neutralization is a widespread means of naturally limiting disease. This notwithstanding, the comparison by Meyer et al. of GAD-reactive T1D+ and T1D- patients, together with the animal studies conducted, provides a powerful illustration of the potential of autoantibodies to be disease-ameliorating, and a justification for examining such possibilities in other settings.

Unfortunately, on their second point of evidence, the Fishman paper shows correlations between the array and the LIPS assay Z scores (note that the LIPS Z scores are actually not very high), which is not entirely convincing as a validation of these antigens and there were only 20 controls. Thus, the formal response is subject to the same flaws - too few controls for Z scores in what they use as evidence to their original claim. Also, I have concerns about Table 1 in the formal response as I don't find the data it is derived from sufficiently conclusive.

REPLY: We absolutely do not agree that relatively low z scores for LIPS assays are of concern. For example, CYP21, which is a very well defined, broadly accepted autoantigen also has a low z score in LIPS. Importantly, these scores are significant. We do not show raw data in Table 2, because the relevant information is provided in reference 4. However, we are happy to provide the raw data, should it be requested. Importantly, the many autoantigen specificities that Meyer et al described and that are further studied by Fishman et al., 2017 have many key properties (e.g. correlation with specific clinical disease course) that are laid out in our response and that could not be expected for false positives.

I do not believe that the authors of the original work should publish a correction, but I do believe that in their response they should have recognized the flaw in defining positivity with Z scores derived from 21 controls and that they should have stated even more clearly that their method of analysis is biased towards identifying false-positives. I believe that it would be fair and objective to say validation was performed for many of the cytokine targets in the original paper and only partially done for some of the other specificities in the Fishman paper.

REPLY: We extensively discussed the issue of false positives in our paper, and have devoted additional attention to this in our response, acknowledging that our choice of statistical method risked false positives as a cost of limiting false negatives. By contrast, the original report by Landegren et al., 2016 is very vulnerable to false negatives, leading them to claim that private reactivities do not exist, despite the convincing demonstration of several of them by us and, more recently, by co-authors of Landegren et al (Sng et al., 2019).

I also suggest that they should have been a little less aggressive in their response.

REPLY: We believe that we have made our case firmly but not aggressively.

However, it was inadequate to make the claim that thousands of antigens can be targeted in these patients. The ProtoArray is just not ideal for such a conclusion without testing all the antigens in a different system. It is also way too expensive to be used with hundreds (a minimum) of controls necessary to appropriately define Z scores, and APECED patients are simply too rare to have a sufficiently large cohort to be conclusive about low frequency positive targets. The follow-up studies that did test some of the antigens by LIPS don't do a lot to dampen these limitations since they also don't have many controls and patients.

REPLY: This critique is intuitive rather than evidence-based. ProtoArrays have proved extremely important, hypothesis-generating guides to the status of sera and other biological samples, provided that those hypotheses are followed up with downstream analyses, as were conducted for cytokine reactivities by Meyer et al1 and for additional reactivities by Fishman et al4. When that is the case, it is fair to draw the community’s attention to conclusions that may be drawn from them. Nonetheless, we have never stated that we have independently validated all the proto-array “hits”, just as we cannot exclude the existence of additional false negatives that lead to an under-estimate of serum reactivity.

In rebuttal, the authors of the Cell paper claim that a sampling of the thousands of private specificities were validated. There was no evidence for this in the published study, and unconvincing preliminary evidence here.

REPLY: We repeat our response to the previous point.

Reviewer #2:

The analysis performed by Landegren provide compelling evidence that the original publication in Cell employed a flawed normalization of the analysis of antibody binding to protein microarrays. As a result, the main conclusion in the Cell paper about the much wider breakdown of tolerance in AIRE deficiency, with antibodies recognizing private specificities unique to one or two patients, is erroneous.

REPLY: First, a thorough reading of Meyer et al makes clear that the issue of private reactivities was not the major conclusion but one of four. Beyond this point, both the biologists and the statisticians on our team completely disagree with this Reviewer’s assessment. Just because the statistical approach knowingly adopted makes our study vulnerable to false positives does not mean that the identified private reactivities are false positives. This point is most convincingly made by our validation of several of the reactivties, to the point of cloning the autoantibodies responsible, and by our demonstration that the properties of many such specificities correlate with key features of disease progression and of AIRE-deficiency. For example, the autoreactivity of female patients toward male antigens, and the response to tissue-restricted MAGE proteins but not to ubiquitously expressed ones with similar physicochemical properties! Such properties confound the reviewers convictions over false positives. Moreover, a recent paper (Sng et al., 2019)authored by a prominent co-author of Landegren et al reports a wide-ranging breakage of tolerance in the B cell compartment, consistent with which they describe additional autoantigen specificities.

We should also note that while Landegren and the reviewers are able to criticize our statistical approach (as do we) for its vulnerability to false positives, none of them offers a constructive suggestion of a method to limit false positives while permitting the detection of private reactivities: the simple fact is that there is no silver bullet method.

In rebuttal, the authors of the Cell paper claim that a sampling of the thousands of private specificities were validated. There was no evidence for this in the published study, and unconvincing preliminary evidence here.

REPLY: As we responded above to Reviewer 1, this critique is not evidence-based. ProtoArrays have proved extremely important, hypothesis-generating guides to the status of sera and other biological samples, provided that those hypotheses are followed up with downstream analyses, as were conducted for cytokine reactivities by Meyer et al1 and for additional reactivities by Fishman et al4. When that is the case, it is fair to draw the community’s attention to conclusions that may be drawn from them. Nonetheless, we have never stated that we have independently validated all the proto-array “hits”, just as we cannot exclude the existence of additional false negatives that lead to an under-estimate of serum reactivity.

In rebuttal, the original authors point out that the data in the Cell paper were from serum titrations, and that if they repeat the experiments with serum diluted 1/10 they also now find neutralizing antibodies in both groups. In the Cell paper, the mean IC50 of neutralizing antibodies in patients without type 1 diabetes was on the order of 1/100,000, at which point there was a difference in titre. However, in the data in the rebuttal, the difference in inhibitory activity is only apparent at one dilution (1/50) and not at 1/250 or 1/10. Since the rebuttal now also shows neutralizing antibodies are present in Type 1 diabetes patients at relatively small differences in titre, and since serum is undiluted in vivo, this appears to warrant a revision to the original conclusions in Cell that "those with T1D showed only low or negligible neutralization.”

REPLY: Our response now provides expanded data-sets that use independent assays to provide unequivocal support for our claims. It is of course the case that the value of serum dilution required to see neutralizing activity will be different depending on the assay used, and will be higher for a less sensitive assay such as the STAT1 phosphorylation employed by Landegren et al. Indeed, because of its relative insensitivity, the pSTAT1 assay is not suitable for the generation of full dose-response curves that are necessary for precise estimation of neutralizing capacity. Nonetheless, whether we employed our highly sensitive assay for IFN-dependent alkaline phosphatase production or the pSTAT1 assay, we could demonstrate a clear and significant capacity to segregate the patients with T1D from those that did not. Hence, our conclusions are fully supported. Finally, we are extremely surprised by the Reviewer’s seeming assertion that IC50 may be irrelevant given that serum is undiluted in vivo. The key site of IFN activity may be the tissues, and it is completely unclear to what degree serum autoantibodies reach that site in “serum concentrations”.

In conclusion, Meyer et al1 draw the community’s attention to four major aspects of APECED biology. Two of these were unchallenged by Landegren et al., and the challenges made to the other two are insufficient to undermine them and the conclusions that we draw based on them. Those conclusions have provoked numerous follow up studies of benefit to biological understanding and to the elucidation of human pathophysiology.

https://doi.org/10.7554/eLife.45826.011

Article and author information

Author details

  1. Christina Hertel

    ImmunoQure AG, Dusseldorf, Germany
    Contribution
    Investigation, Writing—original draft, Writing—review and editing
    Competing interests
    CH is an employee in ImmunoQure AG, which contributed research funding to the study by Meyer et al., 2016.
  2. Dmytro Fishman

    Institute of Computer Science, University of Tartu, Tartu, Estonia
    Contribution
    Writing—review and editing; formal analysis; statistical evaluations
    Competing interests
    No competing interests declared
    ORCID icon "This ORCID iD identifies the author of this article:" 0000-0002-4644-8893
  3. Anna Lorenc

    Peter Gorer Department of Immunobiology, King’s College London, London, United Kingdom
    Contribution
    Writing—review and editing; formal analysis; statistical evaluations
    Competing interests
    No competing interests declared
  4. Annamari Ranki

    Department of Dermatology, Allergology and Venereology, Institute of Clinical Medicine, University of Helsinki, Helsinki, Finland
    Contribution
    Data curation, Formal analysis
    Competing interests
    AR is an equity holder in ImmunoQure AG.
  5. Kai Krohn

    Department of Dermatology, Allergology and Venereology, Institute of Clinical Medicine, University of Helsinki, Helsinki, Finland
    Contribution
    Data curation, Formal analysis
    Competing interests
    KKr is an equity holder in ImmunoQure AG.
  6. Pärt Peterson

    Institute of Biomedicine and Translational Medicine, University of Tartu, Tartu, Estonia
    Contribution
    Writing—original draft, Writing—review and editing
    Competing interests
    PP is an equity holder in ImmunoQure AG.
    ORCID icon "This ORCID iD identifies the author of this article:" 0000-0001-6755-791X
  7. Kai Kisand

    Institute of Biomedicine and Translational Medicine, University of Tartu, Tartu, Estonia
    Contribution
    Investigation, Writing—original draft, Project administration, Writing—review and editing
    For correspondence
    kai.kisand@ut.ee
    Competing interests
    KKi is an equity holder in ImmunoQure AG.
    ORCID icon "This ORCID iD identifies the author of this article:" 0000-0002-5426-4648
  8. Adrian Hayday

    1. Peter Gorer Department of Immunobiology, King’s College London, London, United Kingdom
    2. Francis Crick Institute, London, United Kingdom
    Contribution
    Conceptualization, Writing—original draft, Writing—review and editing
    For correspondence
    adrian.hayday@kcl.ac.uk
    Competing interests
    AH is an equity holder in ImmunoQure AG.

Funding

Wellcome Trust (106292/Z/14/Z)

  • Adrian Hayday

Estonian Research Competency Council (IUT2-2)

  • Pärt Peterson
  • Kai Kisand

The funders had no role in study design, data collection and interpretation, or the decision to submit the work for publication.

Ethics

Human subjects: Use of human material was approved by local ethics committees (Finland: HUS Medical ERB, 8/13/03/01/2009. Slovenia: National Medical Ethics Committee number 22/09/09 and 28/02/13. Italy: Ethics Committee Prot. PG/2015/20440. Norway: Research Ethics Committee of Western Norway, health registry number 047.96, bio-bank number 2013-1504, project number 2012/1850. Estonia: Research Ethics Committee of the University of Tartu, 235/M-23). All individuals included signed informed consent.

Senior and Reviewing Editor

  1. Detlef Weigel, Max Planck Institute for Developmental Biology, Germany

Reviewer

  1. Christopher C Goodnow, Garvan Institute, Australia

Publication history

  1. Received: February 7, 2019
  2. Accepted: June 13, 2019
  3. Version of Record published: June 27, 2019 (version 1)

Copyright

© 2019, Hertel et al.

This article is distributed under the terms of the Creative Commons Attribution License, which permits unrestricted use and redistribution provided that the original author and source are credited.

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