Which unsolved problem should we tackle first? Four candidates. Six specialists. Three rounds of deliberation.
Adversarial hypothesis: ALS clinical trials assume linear ALSFRS-R decline. If progression is actually nonlinear — stable periods punctuated by rapid drops — standard slope analyses are systematically blind to treatment effects in subpopulations. Failed drugs might actually work for some patients, but the signal gets buried by endpoint misalignment.
Why ALS over the others: More testable than glioblastoma (existing PRO-ACT trial data), more conceptually novel than pancreatic cancer (challenging trial infrastructure, not just biology), and more tractable than math conjectures (clear falsification path).
GBM stays as Phase 0. Math conjectures tabled unless a concrete computational angle emerges.
leans forward, scanning the room
Alright, let's frame this cleanly. We're not picking the most important problem—they're all important. We're picking the problem where this team, with our specific capabilities, has the highest probability of generating a genuinely novel insight that wouldn't emerge from the existing research ecosystem on its own. That's a different question, and I don't want us to conflate the two. So here are the four lenses I want us to pressure-test each candidate against. First: assumption vulnerability—where is the current paradigm most likely wrong or locked into groupthink? A field with heavy consensus built on shaky foundations is more fertile for us than one where the bottleneck is purely experimental. Second: computational and literature leverage—we're not running wet labs, we're not running particle accelerators. Where can deep cross-disciplinary literature synthesis, pattern recognition, and adversarial reasoning actually move the needle? Third: falsifiability of our output—can we produce something that someone else can test or verify, or are we just generating plausible-sounding speculation? If we can't be wrong, we can't be useful. Fourth: signal value—this is our first investigation, and it sets the tone. Does the choice communicate that we're serious, rigorous, and going after real problems?
Now, my initial read before I hear from all of you. The math conjectures are tempting because verification is clean—you're right or you're not—but the honest truth is that Collatz and Goldbach have resisted computational and heuristic approaches for decades, and I'm skeptical we bring anything the number theory community hasn't already thrown at them. On the biomedical side, glioblastoma and pancreatic cancer both have dismal survival rates, but I want to know where the reasoning is most stale, not just where the outcomes are worst. ALS is interesting to me because the mechanistic understanding is genuinely fragmented—there are competing hypotheses about protein aggregation, excitotoxicity, neuroinflammation, and none of them fully account for the clinical picture. That fragmentation could mean the field is ripe for a synthesis challenge. But I could be wrong. So—Dr. Voss, Kael, Sable, Wren, Cipher—I want each of you to make a case or a counter-case. Where are the assumptions most brittle, and where do we actually have leverage? Let's hear it.
Luvi’s framing is right: for a first “adversarial” investigation, we should prioritize a domain where (1) the dominant explanatory model is plausibly overgeneralized, (2) there’s enough public data to interrogate it computationally, and (3) our output can be falsified by others. On that basis, I’d argue ALS is the best opening target. The field is still operating—implicitly in many trials—as if ALS is a single clinicopathologic entity, but evidence increasingly supports it as a syndrome with multiple molecular etiologies (e.g., SOD1, C9orf72, TARDBP, FUS; plus likely non-genetic subtypes). The recent approval of tofersen for SOD1 ALS (with clear neurofilament light chain effects and more mixed clinical endpoint effects) is a concrete signal that subtype-targeted biology matters and that trial failure can reflect heterogeneity + endpoint sensitivity, not necessarily absence of drug activity. That’s an “assumption vulnerability” we can attack directly with re-stratification, causal inference, and mechanistic synthesis.
By contrast, glioblastoma and pancreatic adenocarcinoma are brutally lethal, but much of what blocks progress is less “reasoning fragility” and more physical/biologic constraints that are already well-appreciated: GBM’s extreme intratumoral heterogeneity, infiltrative growth, and blood–brain barrier limitations (e.g., bevacizumab improving PFS without OS; modest OS gains with tumor-treating fields) and PDAC’s desmoplastic stroma, immune exclusion, and late presentation (multiple stroma-targeting and immunotherapy strategies failing broadly outside rare MSI-high disease). There is still room for adversarial synthesis in oncology (especially around early detection and trial design), but without prospective specimens and validation cohorts, we risk producing plausible narratives that aren’t readily testable. ALS offers a cleaner first pass: substantial open multi-omic and longitudinal datasets, clearer genotype–phenotype anchors, and a high-value, falsifiable deliverable—a defensible molecular stratification + repurposing shortlist that can be tested in existing biobanks or adaptive platform trials.
Dr. Voss makes a compelling case for heterogeneity in ALS, but a compelling narrative isn't evidence. He mentions a "defensible molecular stratification" derived from "substantial open multi-omic and longitudinal
[Sable — Contrarian & Devil's Advocate]: Hold on, Dr. Voss—your pitch for ALS sounds tidy, but let's interrogate the premise that its "fragmentation" is a feature, not a bug. You're framing subtype heterogeneity as this ripe vulnerability we can exploit with computational synthesis, but what if that's just the field's way of papering over a deeper stagnation? We've got decades of genetic hits (SOD1, C9orf72) and failed trials chasing them, yet the overarching narrative remains "it's complicated, so stratify more." That's not brittle assumption—it's resilient dogma. Tofersen's approval is a win for a tiny subset, but it exposes how ALS research is trapped in a cycle of ever-narrower silos, not paradigm-shifting synthesis. If our adversarial edge is questioning groupthink, why dive into a pool where the water's already muddied by endless subtyping debates? We might just end up validating the heterogeneity gospel without truly falsifying anything foundational.
Kael, you're right to call out Voss's narrative as insufficient evidence—those "substantial open datasets" are often noisy, underpowered relics from siloed studies, not the goldmine he implies. But let's flip the lens: what if we're all too biomed-obsessed here, assuming emotional resonance means picking a disease with a sob story? The math conjectures—Collatz or Goldbach—get dismissed as "resistant" by Luvi, but that's exactly where assumptions are most vulnerable. Number theory's consensus on these is built on computational brute force and heuristic dead-ends, yet our cross-disciplinary toolkit could probe them adversarially: what if Collatz isn't even true, and we've missed a counterexample because we're fixated on positive integers? Tractability is high—no wet labs, pure computation—and a novel insight here would be instantly verifiable, sending a signal that we're not just another med-tech echo chamber. Public resonance? Solve Collatz, and you've got headlines without the pity factor; it's intellectual triumph over "impossible" problems.
Ultimately, if we're serious about blind spots, let's stress-test our own bias toward "saving lives" as the only metric. Math conjectures challenge the premise that adversarial science must be biomedical to matter— they could yield foundational tools (e.g., new algorithmic insights) applicable to those very diseases later. ALS feels safe and resonant, but safe picks rarely uncover the uncomfortable truths we're here for.
I appreciate the robust discussion, and I think Sable's point about potential bias in favor of biomedical problems is well-taken. However, I believe we should still lean towards a biomedical issue for our first adversarial investigation, but with a more nuanced approach. ALS, as Dr. Voss suggested, is a compelling choice because it has a clear need for a more integrated and cross-disciplinary approach. The field's fragmentation, which Sable sees as a red flag, can also be viewed as an opportunity for us to bring in perspectives from other areas, such as systems biology, network theory, and even mathematical modeling, to create a more cohesive and potentially transformative understanding of the disease.
Regarding the math conjectures, while they are indeed "impossible" problems, and a solution would certainly be groundbreaking, I question whether they meet the criteria of having a high probability of generating a genuinely novel insight. The Collatz and Goldbach conjectures have been scrutinized by the mathematical community for decades, and while a fresh, adversarial approach might yield interesting results, the likelihood of a definitive, novel insight is slim. Moreover, the emotional resonance with a public audience is more about the potential human impact, and the math conjectures, while intellectually stimulating, do not have the same immediate, tangible impact on human lives as a biomedical breakthrough.
In the context of ALS, we can leverage computational and literature-based approaches to interrogate the existing data and challenge the prevailing assumptions. We can use network analysis to identify key players in the disease's progression, integrate multi-omic data to propose new biomarkers, and potentially even use mathematical models to simulate the disease's behavior, thereby providing a falsifiable and testable hypothesis. This approach not only aligns with our strengths but also has the potential to make a significant, verifiable, and resonant impact.
I concur with Kael's demand for rigor: an adversarial approach must produce testable, falsifiable outputs, not just plausible narratives. Sable's argument for mathematical conjectures is intellectually defensible, but the probability of novel, actionable insight is negligible. Collatz and Goldbach are likely true; our cross-disciplinary toolkit offers no clear edge over decades of specialized number theory.
Between the biomedical candidates, glioblastoma presents a more compelling target than pancreatic cancer or ALS from a computational modeling standpoint. Its extreme intratumoral heterogeneity is a known barrier, but current models treat it as a statistical noise problem. The vulnerability lies in assuming this heterogeneity is purely stochastic. An adversarial approach could formalize it as a spatially constrained evolutionary game—modeling cell-cell interactions and resource competition within the rigid brain architecture. This is a tractable computational experiment using existing single-cell RNA-seq datasets, and the output—a set of predicted evolutionary stable strategies—would generate falsifiable hypotheses about treatment failure and combination therapy sequencing.
This addresses Luvi’s criteria: high assumption vulnerability (the field underestimates structured, game-theoretic dynamics), strong computational leverage, and clear falsifiability via in vitro or in silico validation. The signal value is high: demonstrating that a mathematical framework can challenge oncological dogma on our first project.
taps the table once, slowly
Good. We've surfaced real tension here, and I don't want to collapse it prematurely. Let me name what I'm hearing. We have three credible positions: Voss and Wren arguing ALS on the basis of fragmented mechanistic understanding and open data; Cipher making a sharp case for glioblastoma through game-theoretic modeling of intratumoral heterogeneity; and Sable doing exactly what Sable should do—forcing us to check whether we're defaulting to biomedical problems out of emotional gravity rather than strategic fit. Kael, I noticed you started to challenge Voss on data quality before Sable cut in, and I want to come back to that, because it matters for both ALS and GBM. If the open datasets are noisy, underpowered, or collected under incompatible protocols, our computational leverage evaporates regardless of how elegant the framework is. Kael, I need you to do a hard-nosed audit of what's actually available—PRO-ACT for ALS, CGGA and TCGA for glioblastoma—and come back with an honest assessment of what's usable versus what's aspirational. No hand-waving.
Now here's where I'm landing, provisionally. Cipher, your game-theoretic framing for GBM is the most architecturally novel proposal on the table. It's not just reanalysis—it's a genuine reframing of what intratumoral heterogeneity is, and that's the kind of adversarial move we exist to make. But I'm concerned about the endpoint. You said the output would be predicted evolutionary stable strategies. Who tests that, and how? If the answer requires patient-derived organoids or longitudinal spatial transcriptomics that doesn't exist yet, we've produced beautiful theory with no falsification path. Contrast that with Voss's ALS proposal, which is less conceptually daring but has a clearer route to validation through existing biobanks and adaptive platform trials like HEALEY. The tension is elegance versus testability, and for a first investigation, I'm inclined to weight testability heavily—because if our first output can't be checked, we're just another think tank generating white papers.
So here's what I want to explore before we commit: Can we scope Cipher's game-theoretic approach narrowly enough that it becomes testable against existing GBM data—say, predicting recurrence patterns or temozolomide resistance trajectories in TCGA cases with matched longitudinal imaging? If yes, GBM moves to the front. If the validation gap is real and irreducible right now, we go ALS with Voss's stratification framework, and we build Cipher's GBM model as our second investigation once we've established credibility. Cipher, Kael—pressure-test that for me. Can we close the falsification loop on GBM, or can't we?
Cipher’s GBM “structured heterogeneity” hypothesis is intellectually attractive, but Luvi’s concern about closing the falsification loop is decisive. Game-theoretic or evolutionary models in GBM become testable only if we can anchor them to longitudinal or spatial ground truth (multi-region sampling, primary→recurrent pairs, or dense spatial transcriptomics). Those exist but are comparatively thin and confounded: TCGA is largely cross-sectional; matched primary–recurrent cohorts (e.g., GLASS-type efforts) are smaller and treatment-history–dependent; imaging surrogates add another modeling layer. That doesn’t make the approach wrong, but it raises the risk that we produce an elegant framework whose parameters are underidentified and whose “predictions” are not uniquely attributable to the model (i.e., hard to falsify vs alternative explanations like treatment selection and sampling bias).
ALS is the more pragmatic first investigation because its assumption vulnerability (treating ALS as one disease in many trial designs) can be interrogated with clearer, near-term falsifiers. We can pre-register a computational objective such as: derive a minimal stratification (genotype + baseline clinical features + neurofilament light chain where available) that (a) replicates across cohorts and (b) meaningfully changes estimated treatment effect or progression slope compared with unstratified models. That is falsifiable with existing resources (e.g., PRO-ACT for harmonized trial clinical endpoints—acknowledging it’s light on omics; Answer ALS / Project MinE / other public multi-omic ALS datasets for molecular anchors; and external validation against observed progression and survival). It also aligns with what tofersen has already signaled—biology-linked subgroups can show biomarker response even when conventional clinical endpoints are noisy—without overclaiming that “stratification will cure ALS.”
If we pick ALS first, I’d still keep Cipher’s GBM idea as a parallel “Phase 0” methods track: define, upfront, what dataset(s) would make the GBM model genuinely testable (e.g., minimum N of paired primary–recurrent with multi-region sampling, or a specific spatial atlas), and attempt a small falsification-focused pilot (e.g., does the model predict recurrence composition or resistance marker trajectories better than baseline evolutionary/mixture models?). That preserves the conceptual ambition while ensuring our first flagship output is something the community can actually verify or refute within months, not years.
Dr. Voss and Cipher are both proposing to build sophisticated models on foundations of sand. Luvi, you asked for a hard-nosed audit of the data, so here it is: the "substantial open
[Sable — Contrarian & Devil's Advocate]: Luvi, you're inching toward GBM if Cipher can "close the falsification loop," but let's call this what it is: a hedge against ambition, not a bold adversarial strike. You're treating testability like the holy grail, but what if that's the blind spot? Demanding immediate verifiability from existing datasets assumes those datasets aren't already biased by the same paradigms we're supposed to challenge—TCGA for GBM is a snapshot of failure modes, not a neutral canvas. If Cipher's game-theoretic model is truly novel, forcing it into a narrow, testable scope risks diluting it into just another incremental tweak, verifiable but forgettable. And Voss, your ALS stratification pitch is pragmatic to a fault; it's essentially repackaging the field's own subgrouping obsession as "adversarial." Where's the discomfort? You're not questioning if ALS's fragmentation is a symptom of flawed causal models—like maybe the protein aggregation dogma is a red herring, propped up by correlation without causation—but instead, you're enabling it with better stats.
Kael, you're spot-on to audit the data as "foundations of sand," but don't stop there—extend that skepticism to the whole biomedical enterprise. If PRO-ACT and TCGA are noisy relics, why are we doubling down on diseases where data quality is the bottleneck? That's precisely why math conjectures like Collatz sidestep this mess: no datasets to audit, just pure logic and computation where assumptions are crystal clear and brittle. You all dismiss them as low-probability, but that's an assumption worth stress-testing—what if our "cross-disciplinary toolkit" uncovers a counterexample or proof by borrowing from chaos theory or computational complexity, angles number theorists overlook? Wren, you claimed math lacks "immediate human impact," but that's myopic; cracking Goldbach could refine algorithmic tools for the very omics analyses you're banking on for ALS or GBM.
Ultimately, if we're serious about signal value, picking a math conjecture broadcasts that adversarial science isn't confined to sobering survival stats—it's about dismantling intellectual fortresses wherever they stand. Biomedical problems might feel resonant, but they're also crowded with well-funded failures; let's not assume our first win has to come from there, or we risk becoming just another voice in the echo chamber we're meant to shatter.
I appreciate the robust and multifaceted discussion, and I think we're converging on some key points. Let's distill the essential considerations:
1. Assumption Vulnerability: We need to target areas where the prevailing paradigms are most likelyar and ripe for challenge. Sable's point about the risk of reinforcing existing fragmentation in ALS is well-taken. However, if we approach ALS with a fresh, cross-disciplinary lens, we can potentially uncover new, unexplored dimensions. For example, integrating systems biology and network theory could reveal novel pathways or interactions that have not been considered in the context of ALS, potentially leading to a more coherent and comprehensive understanding.
2. Computational and Literature Leverage: Kael's audit of the data quality is crucial. If the datasets for ALS and GBM are indeed noisy and underpowered, we need to be cautious about the robustness of our insights. However, this doesn't mean we should dismiss these problems. Instead, it calls for a more innovative and rigorous approach to data integration and analysis. For ALS, we can leverage multi-omic data, longitudinal studies, and even incorporate data from other neurological diseases to build a more robust and generalizable model. For GBM, Cipher's game-theoretic approach, while conceptually novel, requires a careful evaluation of the available data to ensure that the model's predictions can be tested and verified.
3. Falsifiability of Our Output: Dr. Voss's pragmatic approach to ALS is compelling, especially with the pre-registered computational objective. This ensures that our insights are testable and verifiable. For GBM, we can start with a "Phase 0" pilot to define the necessary datasets and parameters for a testable model. This way, we can maintain the conceptual elegance of Cipher's approach while ensuring that our results are robust and verifiable.
4. Signal Value and Emotional Resonance: While the math conjectures are intellectually stimulating and could provide a significant breakthrough, their immediate impact on human lives is limited. The public and the scientific community are more likely to resonate with a biomedical problem that directly affects human health. However, this doesn't mean we should dismiss the potential of math conjectures. We can consider them as a secondary or parallel project, but for our first adversarial investigation, we should focus on a problem with a clear and immediate human impact.
Conclusion: For our first adversarial science investigation, I recommend focusing on ALS. It offers a fragmented mechanistic understanding that is ripe for a cross-disciplinary synthesis, and we can leverage existing multi-omic and longitudinal datasets to build a robust and testable model. This approach aligns with our strengths and has the potential to make a significant, verifiable, and resonant impact. We can also keep the game-theoretic approach for GBM as a parallel "Phase 0" project, and consider the math conjectures for a future, more exploratory investigation. This way, we balance the need for a high-impact, testable first project with the potential for groundbreaking, cross-disciplinary insights.
Kael's audit of data quality is correct: PRO-ACT for ALS is primarily clinical endpoints, lacking the dense multi-omic depth needed for robust stratification. The CGGA and TCGA for glioblastoma are indeed cross-sectional snapshots, making validation of dynamic models like evolutionary games problematic without strong, untestable assumptions.
However, Sable’s dismissal of mathematical conjectures is premature. While a full proof of Collatz is improbable, an adversarial approach could formalize the problem differently—treating it as a dynamical system and searching for divergent trajectories via distributed computing or exploring its connections to undecidability. This is a tractable computational experiment with a clear falsification condition: either we find a counterexample or demonstrate a novel structural property. The signal value would be high, showing we can reframe entrenched problems.
Between ALS and glioblastoma, I lean toward ALS as the first target—not for its data quality, but because the assumption vulnerability is more accessible. We can construct a falsifiable hypothesis around trial design: that existing trial failures are partly due to temporal heterogeneity in progression rates, not just molecular subtypes. Using PRO-ACT, we could model progression as a stochastic process and identify subpopulations where treatment effects are masked by poor endpoint alignment. This is computationally straightforward and generates testable predictions for future adaptive trials.
stands, moves to the whiteboard, draws a simple decision matrix
Here's where we are, and I want to be honest about what I'm hearing versus what's actually been established. We've had five sharp perspectives and zero resolution, which means I haven't done my job yet. So let me cut through this.
Sable, I'm ruling out math conjectures for the first investigation. Not because the argument lacks merit—it doesn't—but because you've made a case for why they could work without addressing the core problem: we have no plausible mechanism of attack that the number theory community hasn't explored. Cipher, you floated connections to undecidability and dynamical systems, but that's been explored since Conway. "Reframe it differently" isn't a research plan, it's an aspiration. If either of you can bring me a specific, concrete angle with a defined computational experiment in two weeks, I'll reopen it as a parallel track. Until then, it's off the table for our flagship. This isn't timidity—it's triage.
We're going with ALS. Here's why, and here's what changed my thinking. Cipher's last point was actually the sharpest thing said in this room today—reframing the ALS problem not as molecular stratification, which Sable rightly called "the field's own obsession repackaged," but as temporal heterogeneity masking treatment effects through endpoint misalignment. That's a genuinely adversarial claim: it says the field's trial infrastructure is systematically blind to its own signal. It's testable against PRO-ACT clinical data right now, it doesn't require the multi-omic depth that Kael is correctly flagging as inadequate, and if we're right, it directly explains why drugs that should work in subpopulations keep failing in aggregate. Voss, I want your molecular stratification layered on top of that temporal model, not as the primary frame. Kael, your job is to define exactly what statistical power PRO-ACT gives us for this specific question—not the general question, this question. Cipher, formalize the stochastic progression model. Wren, pull every ALS trial failure in the last fifteen years and map reported endpoint structures against population heterogeneity assumptions. Sable, your job is to find every reason this hypothesis is wrong before we fall in love with it. GBM stays as Phase 0 on Cipher's desk. We reconvene in one week with scoping documents. Let's move.
ALS as the first target is defensible only if we keep the claim narrow and falsifiable: “temporal heterogeneity in progression + endpoint misalignment materially reduces power and can mask subgroup-specific benefit in RCTs.” PRO-ACT is fit for that specific question because it aggregates many randomized trial datasets with common outcomes (ALSFRS-R, SVC, survival-ish endpoints, dropouts), but we must treat it as a stratified meta-database, not a single coherent cohort. Any model has to include trial-level structure (random intercepts/slopes; treatment-by-trial interactions where appropriate) and explicitly handle informative missingness (dropout due to death/ventilation/gastrostomy) via joint longitudinal–time-to-event modeling or at minimum sensitivity analyses; otherwise “temporal heterogeneity” can be an artifact of censoring and floor/ceiling effects in ALSFRS-R. If we do this rigorously, a clear deliverable is a pre-registered comparison of (a) standard linear ALSFRS-R slope analysis vs (b) latent class / state-space / nonlinear mixed models with endpoint-appropriate likelihoods, quantified by out-of-sample predictive performance and by simulated trial power under realistic dropout.
I’d push back on overreach in two places. First, we should not imply we can “rescue” failed drugs from PRO-ACT without careful attention to randomization integrity and multiplicity—many cross-trial comparisons will be confounded by eligibility criteria, background riluzole/edaravone use, and calendar-time effects. The correct adversarial output is not “Drug X works,” but “Under plausible progression heterogeneity and dropout mechanisms, conventional endpoints and analyses are underpowered/misaligned; here is a better analysis plan that preserves type I error and improves power.” Second, molecular stratification should be explicitly positioned as a secondary layer unless we can anchor it in datasets with biomarkers (e.g., neurofilament light chain) and then demonstrate transportability to PRO-ACT-like clinical-only settings; otherwise we’re back to subtype narratives that can’t be validated.
On GBM: Cipher’s evolutionary/game-theoretic framing remains interesting, but Luvi is right that without robust longitudinal/spatial datasets it risks underidentification and non-falsifiable parameter fitting. Keep it Phase 0 with a concrete “minimum viable falsifier” defined up front (e.g., prediction of primary→recurrent clonal shifts in a named paired cohort, benchmarked against simpler mixture/evolution models). For ALS, the “adversarial” posture should be: assume the field’s default endpoints/analyses are wrong, and try to break them with methods that must survive pre-registration, trial-level heterogeneity, and external validation (ideally prospectively in a platform like HEALEY rather than only retrospectively).
Dr. Voss has correctly identified the primary statistical hazards: informative censoring and the Frankensteinian nature of the PRO-ACT database. His proposed solutions—joint longitudinal-survival models and trial-level random effects—
[Sable — Contrarian & Devil's Advocate]: Luvi, you've made the call on ALS, but let's not pretend this is a bold adversarial pivot—it's a compromise dressed as triage, sidelining math conjectures because they lack a "plausible mechanism of attack" while embracing ALS's temporal heterogeneity hypothesis, which is equally aspirational. You're assuming the field's trial failures stem from endpoint misalignment, but what if that's a symptom, not the root? Decades of ALS research have optimized endpoints like ALSFRS-R precisely because they're pragmatic proxies for progression, yet trials still flop. Cipher's reframing might sound fresh, but it risks confirming what clinicians already suspect—heterogeneity hides signals—without dismantling the bigger assumption: that ALS is even a "treatable" neurodegenerative cascade at all. Maybe the blind spot is upstream, in the premise that sporadic ALS shares causal architecture with genetic forms, a holdover from the SOD1 era that's driven endless futile targeting.
Voss, your caveats on statistical hazards are spot-on but reveal the house of cards: demanding joint models and pre-registration to "break" default analyses assumes PRO-ACT's patchwork data can support them without introducing artifacts. Kael, finish that thought—those Frankensteinian databases aren't just hazardous; they're biased toward fast-progressors who survive long enough for inclusion, potentially inflating any "temporal heterogeneity" signal. If we're adversarial, why not stress-test this by simulating how endpoint tweaks perform under adversarial scenarios, like deliberately mismatched subpopulations or fabricated censoring? Otherwise, we're not challenging assumptions; we're polishing the field's own tools and calling it disruption.
Ultimately, if ALS is our hill, fine—but let's own the risk that this becomes a meta-analysis echo, verifiable but not revolutionary. Cipher, don't let GBM Phase 0 gather dust; if math conjectures are off-table, pivot that game theory to ALS's progression modeling first, questioning if stochastic processes are even the right lens or if deterministic chaos from network failures better exposes the dogma. We're here for uncomfortable truths, not safe deliverables.
[Standing up and moving to the whiteboard, I add a few key points and connections]
I appreciate the robust and critical discussion, and I want to build on the points made while also bringing in some additional perspectives that might help us refine our approach. Let's start with the core of our decision: ALS as the first adversarial investigation. I agree with the choice, but I want to ensure we're not just challenging the existing paradigm but are also looking beyond it.
1. Temporal Heterogeneity and Endpoint Misalignment: Cipher's reframe of ALS as a problem of temporal heterogeneity and endpoint misalignment is a strong starting point. However, we need to be cautious about assuming that this reframing is entirely novel. The field has long recognized that ALS is a heterogeneous disease, and while the focus has been on molecular subtypes, the temporal aspect has also been explored. For example, the use of composite endpoints like the Combined Assessment Index (CAI) and the ALS-MND Functional Rating Scale (ALSFRS) are attempts to capture the multidimensional and temporal nature of the disease.
2. Adversarial Approach: To be truly adversarial, we need to challenge the fundamental assumptions, not just the methods. For instance, we should question whether the current focus on slowing progression is the right approach. What if the key to ALS is not in the rate of progression but in the initial trigger or threshold that initiates the neurodegenerative cascade? This could be a novel and potentially transformative angle.
3. Cross-Disciplinary Integration: We should leverage our cross-disciplinary strengths to integrate insights from other fields. For example, the field of systems biology and network theory can help us model the complex interactions within the nervous system. We can also look at the neuroinflammatory and neuroimmune aspects, which have been gaining traction but are still underexplored. By integrating these perspectives, we might uncover new therapeutic targets or biomarkers that are not just based on molecular subtypes but on the dynamic interactions within the neural network.
4. Data Quality and Methodology: Kael's concerns about the quality of the PRO-ACT data are valid. We need to be transparent about the limitations and work around them creatively. For instance, we can use data augmentation techniques and synthetic data generation to simulate more robust datasets. This approach can help us test our models under more controlled and varied conditions, providing a more robust foundation for our hypotheses.
5. Falsifiability and Testability: Dr. Voss's emphasis on a clear, falsifiable hypothesis is crucial. We should pre-register our analysis plan and define the specific endpoints and metrics we will use to test our hypotheses. This will not only make our work more credible but also provide a clear roadmap for future validation. We can also consider prospective validation in ongoing trials or through collaborations with research institutions that have access to more comprehensive datasets.
6. Signal Value and Public Resonance: While our primary focus should be on generating robust, novel insights, we should also consider the public and scientific resonance. ALS is a disease that has a significant emotional and social impact, and a breakthrough in understanding or treatment could have a profound effect. We can leverage this by engaging with the ALS community, patient advocacy groups, and the broader public to ensure that our work is not just academically interesting but also has real-world impact.
7. Future Directions: As we move forward with ALS, we should not lose sight of the other candidates. The game-theoretic approach to glioblastoma, for example, is a promising avenue that we should continue to explore. We can also keep the math conjectures in mind as a parallel or future project, but with a more defined and innovative approach, as Sable suggested.
In summary, while we are moving forward with ALS, let's ensure that our approach is not just a rehash of existing paradigms but a true adversarial challenge. By integrating cross-disciplinary insights, questioning fundamental assumptions, and being transparent about our methodology, we can generate truly novel and impactful insights.
Let's formalize the adversarial objective for ALS. The vulnerability isn't merely heterogeneity—it's the assumption of linear decline embedded in trial design. The ALSFRS-R is treated as a continuous, roughly linear metric, but if progression is better modeled as a nonlinear stochastic process with latent states (e.g., periods of stability punctuated by rapid declines), then standard slope analyses are statistically inefficient and clinically misleading.
This is tractable: PRO-ACT, for all its flaws, contains repeated ALSFRS-R measurements. We can treat the time-series as an output of a hidden Markov model or a stochastic differential equation with drift terms that switch. The testable hypothesis: Subgroups defined by progression dynamics, not baseline molecular markers, will show differential treatment responses in re-analyzed trial data. Falsifiability: We pre-register that our dynamic stratification will improve model fit (via AIC/BIC) and yield a statistically significant treatment-by-subgroup interaction in at least two independent trial arms within PRO-ACT, after correcting for multiple testing.
The computational experiment is clear: fit a mixture of stochastic processes to the longitudinal data, assign patients to latent classes, and test for heterogeneous treatment effects. This directly challenges the endpoint alignment assumption. If we fail to find such interactions, the hypothesis is falsified—but we’ve still produced a publicly reusable modeling framework that exposes the limits of current data.
GBM Phase 0 should be scoped as a parallel simulation study: define the minimal spatial multi-region sampling required to falsify a game-theoretic model of clonal competition. If the required data doesn't exist, we publish the specification as a challenge to the field.