As of April 29, 2026, I would triage these as **2 near-term translational programs**, **3 conditional/retool programs**, and **2 not-ready programs**.
| Rank | Hypothesis | Feasibility | Development Call |
|---|---:|---|
| 1 | **GBA1/GCase in PD** | High | Best drug-development case |
| 2 | **C9orf72 RNA/DPR biology** | Moderate-high biology, hard clinic | Worth pursuing, but not DPR-only |
| 3 | **Mitophagy/NAD in PD** | Moderate | Trialable, but mechanism must be sharpened |
| 4 | **TDP-43 LLPS/proteostasis** | Moderate-low | Strong biology, poor druggability today |
| 5 | **TREM2-SYK agonism** | Biologically strong, clinically weakened | Reposition or combine, not standalone AD bet |
| 6 | **Astrocyte senescence in ALS** | Low-moderate | Needs causal validation before clinical spend |
| 7 | **Tau muscarinic BBB transcytosis** | Low | Not development-ready |
**1. GBA1/GCase: most feasible**
Druggability is strong: enzyme enhancement, pharmacological chaperones, substrate reduction, gene therapy, and lysosomal-biogenesis strategies are all plausible. The best path is **GCase restoration or substrate correction**, not broad TFEB activation first. Ambroxol has human CNS exposure and target-engagement data, and a 2025 PDD trial found it safe/tolerable but not efficacy-positive on primary outcomes. A completed GBA-PD trial is listed without posted results yet, so this remains clinically alive but not proven.
Biomarkers are unusually good for neurodegeneration: genotype enrichment, CSF/plasma GCase activity, glucosylceramide/glucosylsphingosine, alpha-syn seed amplification assays, NfL, DAT-SPECT, MDS-UPDRS, and cognitive endpoints for GBA-PD/PDD. Models should include human GBA1 iPSC dopaminergic neurons, lysosomal flux assays, alpha-syn seeding models, and aged knock-in or human alpha-syn models rather than DAT-Cre knockout alone.
Clinical constraints: recruit **GBA1-PD**, stratify severe versus mild variants, and design for 12-24 months. Cost: roughly **$10-25M** for IND-enabling/phase 1 if repurposed small molecule, **$40-120M** through a serious phase 2, more for gene therapy. Timeline: **2-4 years** to a credible phase 2 readout if using an existing CNS-penetrant agent; **6-9 years** for novel biologic/gene therapy.
**2. C9orf72 RNA/DPR: strong target, sobering clinical history**
Druggability is real because ASOs can hit CNS RNA, and the tofersen precedent in SOD1-ALS supports genetically targeted ALS development using biomarkers such as NfL. But C9orf72 is not a simple “lower DPRs and win” program. BIIB078 and WVE-004 both showed the key warning: target/DPR biomarker movement did not translate into clinical benefit, and WVE-004 was terminated despite robust poly(GP) reduction.
The next viable approach should separate **sense RNA, antisense RNA, DPRs, and C9orf72 haploinsufficiency**. A pure RAN-translation small molecule like furamidine is too nonspecific and likely unattractive unless it shows clean CNS exposure and safety. Better druggability: allele-selective ASOs, RNA binders, repeat-targeted degradation, or combined RNA-lowering plus functional rescue.
Biomarkers: CSF poly(GP), NfL, repeat RNA foci in patient-derived systems, DPR immunoassays, TDP-43 mislocalization markers, neurophysiology, ALSFRS-R slope, and FTD cognitive measures. Timeline/cost: **$30-80M** to optimized candidate plus early ALS/FTD biomarker trial; **$150-300M+** to pivotal development. Main risk is not delivery; it is whether the target node is sufficient.
**3. Mitophagy/NAD in sporadic PD: trialable but mechanistically diffuse**
Nicotinamide riboside and related NAD approaches are druggable, orally deliverable, and comparatively safe. NADPARK showed oral NR increased brain NAD in PD over 30 days and produced metabolic signals, but that is not disease modification. Urolithin A is similarly feasible but not yet a PD disease-modifying therapy.
The key development issue is mechanism. “Mitophagy induction” can become a catch-all. A credible program needs proof of **mitophagy flux in human dopaminergic neurons**, not just blood NAD metabolites. Biomarkers should include 31P-MRS or PET metabolic measures, mitochondrial DNA damage/copy number, complex I-linked signatures, alpha-syn SAA, NfL, inflammatory markers, and wearable motor measures.
Best trial: early untreated PD, 12-18 months, biomarker-enriched for mitochondrial impairment. Cost: **$15-40M** for a phase 2 repurposed-nutraceutical-style program; **$80-150M** for a regulated novel mitophagy drug. Safety is manageable for NR but less clear for potent mitophagy activators because excessive mitochondrial clearance could harm high-energy neurons.
**4. TDP-43 LLPS/proteostasis: compelling but not yet product-shaped**
TDP-43 is central to ALS/FTD, but LLPS restoration is hard to drug cleanly. Directly modulating condensate behavior risks broad effects on RNA granules, splicing, stress responses, and nuclear TDP-43 function. Chaperone overexpression is scientifically useful but therapeutically awkward: gene therapy dose, cell-type targeting, proteostasis overload, and chronic safety are major barriers.
Better tractable approaches: restore nuclear TDP-43 function, suppress cryptic exon pathology, improve autophagy/proteostasis selectively, or target downstream RNA-splicing consequences. Biomarkers are improving: CSF NfL, TDP-43 seeding/fragment assays if validated, cryptic exon signatures such as STMN2, neurofilament, EMG, respiratory decline, and iPSC motor-neuron survival.
Timeline: **3-5 years** for a credible preclinical package; **7-10+ years** to meaningful clinical proof unless a highly specific RNA or biomarker-linked approach emerges. Cost: **$25-75M** to candidate/IND; **$150M+** to phase 2 ALS efficacy attempt.
**5. TREM2-SYK: biology survives, standalone AD therapy weakened**
TREM2 is druggable with antibodies and perhaps small molecules, and biomarkers are strong: CSF soluble TREM2, osteopontin, microglial PET where available, amyloid/tau PET, plasma p-tau217, NfL/GFAP, and synaptic markers. But the 2026 AL002 phase 2 trial in early AD showed CNS target engagement and pharmacodynamic response yet missed the CDR-SB primary endpoint; MRI changes resembling ARIA were common. That sharply lowers standalone feasibility.
The most realistic future is **stage-specific or combination therapy**, possibly with amyloid lowering, tau-directed therapy, or genotype/pathology enrichment. Safety requires careful ARIA-like MRI monitoring and inflammation/synapse-loss surveillance. Cost is high: antibody AD trials are typically **$100-300M** through phase 2b and **$500M+** for phase 3. Timeline: **5-8 years** for a redesigned clinical signal. I would not fund another broad early-AD TREM2 agonist monotherapy without a sharper responder hypothesis.
**6. Astrocyte senescence in ALS: preclinical only for now**
Druggability exists in the abstract: senolytics, SASP suppression, p16/p21 pathway modulation, BCL-2 family targeting, IL-6/STAT3 inhibition. But systemic senolytics are blunt, and navitoclax-class toxicity, platelet effects, immune effects, and CNS penetration are serious concerns. Removing astrocytes in ALS could also remove compensatory trophic support.
This needs causal validation before clinical development: spatial single-cell evidence that senescent astrocytes precede motor-neuron loss, astrocyte-specific genetic clearance, and rescue of NMJ integrity/survival in multiple ALS models beyond SOD1G93A. Biomarkers would include CSF SASP proteins, GFAP, NfL, inflammatory panels, PET glial imaging, and cell-source-resolved markers if available.
Timeline/cost: **$5-15M** for rigorous validation; **$30-80M** to an early CNS senolytic program. I would not start patient dosing based on current rationale.
**7. Tau muscarinic BBB transcytosis: not ready**
This is the weakest. LRP1/heparan sulfate tau uptake and neuronal-network propagation are plausible; muscarinic M1/M3-mediated BBB transcytosis is not yet a solid therapeutic axis. CHRM1/CHRM3 antagonism or deletion has unacceptable CNS, autonomic, vascular, and cognitive confounds for AD.
Before drug development, the required experiment is endothelial-specific perturbation with peripheral labeled tau and direct CNS-entry quantification. The proposed intracerebral seed experiment does not test the BBB claim. Biomarkers and models are also problematic: tau PET in mice is difficult, and peripheral tau does not automatically imply pathogenic CNS import.
This is a **research hypothesis**, not a translational program. Cost to validate: **$2-8M**. Timeline: **2-3 years** to decide whether to kill or reframe. Clinical development should not begin.
**Bottom Line**
Fund first: **GBA1/GCase** and a redesigned **C9orf72 RNA program**.
Fund selectively: **mitophagy/NAD in PD**, but only with neuron-relevant flux biomarkers.
Keep in discovery: **TDP-43 LLPS** and **astrocyte senescence**.
Reposition: **TREM2**, because AL002 weakens the monotherapy case.
Do not develop yet: **tau-muscarinic BBB transcytosis**.
Sources checked: AL002 phase 2 Nature Medicine 2026, BIIB078 Lancet Neurology 2024, WVE-004 ClinicalTrials.gov/AFTD reports, NADPARK Cell Metabolism 2022, ambroxol PDD JAMA Neurology 2025, tofersen FDA/NINDS summaries.