Mimicry Test or Damage Marker? A Consensus-Calibrated Longitudinal Protocol for Post-Infectious Autoimmune Encephalitis

Patients who survive a viral brain infection sometimes relapse weeks later with a second, autoimmune brain disease — the immune system, having cleared the virus, turns against the patient's own neurons. A landmark study profiled the antibody contents of paired cerebrospinal fluid and blood from such patients and found a viral antibody signature that predicts the autoimmune relapse with striking accuracy; yet, puzzlingly, those viral antibodies showed no sequence similarity to the neural target, undermining the textbook explanation ("molecular mimicry," where a pathogen's proteins resemble the body's own) in favor of mechanisms like bystander immune activation. Meanwhile, the clinical cohorts that track these patients rarely follow them long enough to see late relapses and deaths, and no expert consensus has ever defined when, how often, or in which fluid compartment recovering patients should be monitored. This proposal builds a single connected pipeline out of these four strands: a mechanism-resolving assay comparison (mimicry vs. bystander), a survival model that handles short follow-up honestly, and a formal expert consensus process that converts both into a standardized monitoring protocol.

The core new object is what we call a consensus-calibrated monitoring protocol: a Delphi-defined schedule of paired CSF/serum sampling timepoints, each with a pre-registered decision rule, whose intervals and thresholds are chosen not by intuition but by optimizing a survival model's power under the truncated follow-up that real cohorts actually achieve. No existing work combines even two of these elements for post-infectious neuroimmunology: the profiling-plus-mimicry work stops at prediction without mechanism resolution or consensus (Kreye et al.), the outcome cohorts stop at classical regression without accounting for what their short windows hide (Zhong et al.; Zhong et al.), and the Delphi studies standardize temporal criteria in other diseases while explicitly calling for fluid biomarkers they never integrate (Skrobot et al.).

Core Claim

We claim three things, in decreasing order of confidence. First, that the "mimicry versus bystander" question in post-herpes simplex encephalitis (HSE) autoimmune brain disease can be settled empirically by comparing antibody binding across assay formats that preserve or destroy protein shape: if the predictive viral antibodies are true conformational mimics, they will bind folded human NMDAR proteins in cell-based and wet-protein arrays and lose binding in denatured linear formats; if they are damage markers, they will bind viral peptide regardless of format and never bind the neural antigen in any format. Second, that the 18-month median follow-up in existing cohorts materially biases relapse and mortality estimates, and that a survival model designed for heavily censored small cohorts — used in-context on the combined published cohorts — can produce calibrated late-risk estimates where Cox regression cannot. Third, that a Delphi panel of neuroimmunologists, given the assay evidence and the survival curves as structured feedback between rounds, can converge on a monitoring schedule with explicit timepoints, compartments, and risk thresholds — the missing standardization that every paper in this space lists as a limitation.

The mimicry tension is real and unresolved in the literature. Kreye et al. found that antibodies against five HSV-1 UL42/UL48 peptides in CSF predict secondary anti-NMDAR encephalitis with 75% sensitivity and >99% specificity (odds ratio 209), yet exhaustive sequence analysis showed no homology to NMDAR subunits — so either the mimicry is conformational (invisible to sequence search) or it is not mimicry at all. On the other side, Fu et al. provide the proof-of-concept that genuine cross-reactivity exists and is pathogenic: in lupus, antibodies to a bacterial biofilm peptide cross-react with a human renal enzyme and worsen kidney disease — but that work is serum-based, cross-sectional, and outside the nervous system. Our proposal operationalizes the distinction for the neural case instead of assuming either answer.

Research Program

The program has three linked workstreams.

The first workstream is mechanism resolution. We take the HSV-1 UL42/UL48 signature peptides and the human NMDAR subunit extracellular domains and test antibody binding in a graded panel of assay formats that bracket epitope structure: linear peptide ELISA (destroys shape), cell-free wheat-germ wet protein arrays (preserves hydration and folding, per the A-Cube methodology of The Autoantibody Array Assay, which detected anti-OJ antibodies that ELISA and immunoprecipitation both missed), and full cell-based assays expressing NMDAR in native conformation on human cells (the diagnostic gold standard per Lai et al. and He et al.). Patient sera and CSF come from the post-HSE cohort structure of Kreye et al. (13 HSE patients who developed secondary autoimmune encephalitis, 10 who did not, 70 autoimmune-encephalitis patients without HSE, 40 multiple sclerosis controls). We additionally run computational structural alignment between the UL42/UL48 peptides and folded NMDAR domains, and cross-check with the protein language model approach of Ofer & Linial, which distinguishes human from viral proteins at 99.7% ROC AUC — their 9.48% "viral-reads-as-human" error class is exactly the candidate-mimic set we would test first in the wet assays, since those misclassified viral proteins correlate with chronic infection and immune evasion. The decisive outcome is a two-by-two: binding to folded human antigen (yes/no) against binding to viral peptide independent of format (yes/no). Conformational mimicry requires the first; a bystander or damage-marker account predicts only the second.

The second workstream is honest survival modeling under short follow-up. We pool the published autoimmune encephalitis outcome data — 100 patients with anti-NMDAR, anti-LGI1, and anti-GABA_B R subtypes, median follow-up 18 months, 26% relapse, 15% mortality (Zhong et al.; Zhong et al.) — and re-analyze them with the in-context survival model SurvivalPFN (Qi et al.), which predicts full posterior survival curves in a single forward pass without task-specific training, an advantage precisely because our cohort is small. The key methodological move is a simulation-based power audit: we treat the observed 18-month window as a censoring regime, generate synthetic cohorts with known late-relapse kinetics under several hazard assumptions, truncate them to the empirical follow-up distribution, and measure how much the truncated Cox estimates of the original studies (e.g., the hazard ratio of 2.447 for delayed immunotherapy) are biased and how much of the tail the amortized model recovers. This directly addresses the authors' own caveat that 6-to-18-month windows likely underestimate late relapse and mortality. The audit also produces something the Delphi panel needs: for each candidate monitoring interval (3, 6, 12, 24 months), the minimum detectable relapse-risk change given realistic sample sizes — turning "follow-up was too short" from a limitation into a design parameter.

The third workstream is the Delphi consensus process. We convene an international panel of neuroimmunologists and run a modified three-round Delphi, following the structural template of Dombrowski et al. (75 experts, 25 countries, 3 rounds, consensus at 75%) and the a priori 67% threshold of the VICCCS study (Skrobot et al.). Between rounds, the panel receives not just the usual aggregate medians and interquartile ranges but the quantitative artifacts of workstreams one and two: the assay-format binding matrix (mimicry vs. bystander evidence) and the power-audit curves (what each follow-up interval can and cannot detect). This is the crucial difference from prior consensus exercises: Skrobot et al. codified temporal windows for post-stroke dementia but had no biofluid evidence to anchor them, and Dombrowski et al. frankly conceded that most of their statements remained Grade E expert opinion. Our design injects empirical constraints into the deliberation, so that consensus statements are rated against the detectability limits the data actually support. The output is a protocol specification: post-HSE sampling at defined weeks, paired CSF-and-serum requirement (justified by the intrathecal-enrichment evidence of Kubota et al. and Kreye et al.), assay format per timepoint, and pre-specified action thresholds — each statement carrying a consensus percentage and a stated evidence grade.

Proposed Experiments

The experiments are grounded in the cohorts and benchmarks in the file. Experiment one (mechanism) uses the post-HSE biospecimen structure — 309 samples from 133 individuals across four groups — with the graded assay panel above; its readout is the binding matrix, and its pre-registered decision rule is stated in the Core Claim. Experiment two (survival) uses the pooled 100-patient Jilin University cohort outcomes as the empirical anchor, with SurvivalPFN evaluated by Concordance Index and Brier Score on held-out patients under the censoring regimes of the power audit; no reported result found on Lacuna for SurvivalPFN or any survival model applied to CSF autoantibody cohorts, which is precisely the gap this experiment fills. Experiment three (consensus) reports round-by-round agreement percentages, Content Validity Index for each protocol item (following Wake et al.), attrition across rounds, and — the decisive check — whether any statement's final consensus rating changed when the panel saw the power-audit curves, which would demonstrate that evidence injection, not mere iteration, drove the outcome.

Baselines

The naive reference point is current practice: no structured post-infectious monitoring at all, with clinical judgment deciding when to re-test. This is what every cited cohort and case report actually did — Lai et al. followed their post-COVID nodopathy patient only through the acute immunotherapy response, and He et al. followed their post-neurobrucellosis GFAP astrocytopathy case only to discharge. Any protocol that experts rate above "no monitoring" in the Delphi rounds, with better simulated detection power at equal sampling cost, beats this baseline.

The strongest competitor for the mechanism question is the sequence-homology analysis as performed by Kreye et al., which is the only published attempt to adjudicate mimicry in this setting and concluded no homology exists. We will run their exact sequence-alignment approach on the same peptide–antigen pairs as our primary comparison baseline, and beating it means showing that assay-format binding data discriminates cases sequence analysis cannot: specifically, if any HSE-patient antibodies bind folded NMDAR while sequence alignment reports no homology, we have demonstrated conformational mimicry that the strongest existing method is structurally blind to. If no binding appears in any format, we replicate their negative conclusion with an orthogonal method, which still resolves the question more firmly than sequence analysis alone.

For the survival workstream, the strongest baseline is the Cox proportional hazards regression that Zhong et al. used on this very cohort (their delayed-immunotherapy hazard ratio of 2.447 is the number to reproduce and stress-test), and the amortized SurvivalPFN model is compared against it under identical truncation regimes and identical input covariates, with the synthetic ground truth of the power audit as arbiter. The key ablation isolating our consensus ingredient is a Delphi panel run without the evidence injection — standard anonymous iteration with only median feedback, as in Dombrowski et al. — against the same panel given the assay matrix and power curves. If the evidence-injected panel produces tighter, better-calibrated intervals at equal round count, the injection is doing real work; if not, we will report that iteration alone suffices, which would itself be a useful negative result for the emerging literature on AI- and evidence-mediated deliberation (AI Agents and the Future of Deliberation).

Why not just…?

Why not just test serum and avoid lumbar punctures? Serial spinal taps are the single biggest practical obstacle to any monitoring protocol, so a serum-only design would be far easier to sell to a panel. But the literature is unambiguous that serum alone misses intrathecally synthesized antibodies: Kubota et al. and Zhong et al. document serum false negatives from blood-brain barrier dynamics, and the predictive signature in Kreye et al. was defined by CSF enrichment computed from paired samples. That said, this is a real constraint, not a talking point: our protocol therefore specifies paired sampling only at the few timepoints the power audit deems informative, and the Delphi panel explicitly weighs serum-only interim monitoring against paired sampling at sentinel timepoints rather than assuming maximal invasiveness.

Why not just use linear peptide ELISAs? They are cheap, fast, and automated. But the file gives direct evidence they fail exactly where this proposal lives: neural autoantigens like NMDAR carry purely conformational epitopes destroyed by ELISA denaturation (Lai et al.; He et al.), and the A-Cube cell-free arrays caught anti-OJ antibodies that ELISA and immunoprecipitation both missed (The Autoantibody Array Assay). More fundamentally, the ELISA-versus-folded-assay contrast is not a cost we begrudge — it is our mechanism experiment. If the predictive antibodies bind only linear viral peptide and never folded human antigen, the ELISA result itself becomes evidence for the bystander account.

Why not just hold a one-day expert workshop instead of a multi-round Delphi? A workshop is faster, and for producing a protocol document it might genuinely suffice. The file's evidence says it suffices poorly: open committees are documented to converge on the loudest or most senior voice rather than the best argument, which is why the Delphi structure — anonymity, iteration, statistical feedback — was adopted in the first place (Dombrowski et al.; Byrne et al.). Because our claims about which timepoints and thresholds matter are quantitative, we need the item-level agreement indices (Content Validity Index, round-over-round stability) that only a formal consensus process yields; a workshop gives us a document but no measurable consensus. Still, if the field ultimately ignores the protocol, the Delphi machinery will have been overhead — which is why the evidence-injection ablation matters: it tests whether the formal process earns its cost.

Why not just use Cox regression, as the field always has? This is the most serious alternative, and for the original 18-month window it would be adequate. It fails for two reasons our design exploits. First, the question we care about is precisely the tail Cox cannot see: SurvHTE-Bench shows standard models and simple imputation degrade badly once censoring exceeds 70%, a regime our power audit deliberately constructs, and Deep Survival Analysis showed a 73.11% concordance index versus 65.57% for a classical risk score when longitudinal records are sparse. Second, Cox gives point hazard estimates, while the Delphi panel needs calibrated uncertainty about late risk to set monitoring intervals defensibly. The honest counterpoint survives: extrapolation beyond the observed tail rests on distributional assumptions no model can verify, a limitation Qi et al. themselves note. That is why our survival claims are confined to what the synthetic-audit calibration demonstrates, and why the protocol's late timepoints are framed as power-limited surveillance windows rather than predicted-risk statements.

Decisive Checks

The proposal succeeds if the assay matrix cleanly separates conformational mimicry from bystander activation in the post-HSE setting; if the power audit quantifies — for the first time — how much late relapse the standard 18-month window hides, using the 26% relapse and 15% mortality figures of Zhong et al. as the empirical anchor; and if a Delphi panel, given those results, converges on a monitoring protocol whose every timepoint is justified by a detectability curve rather than by habit. It fails informatively if the panel converges without needing the evidence, or if the survival model's tail extrapolations prove uncalibrated — either failure would sharpen the field's next attempt, and both are built into the design as reported outcomes rather than risks to be buried.

References

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