Orthogonal

Stated Theory of Change

Orthogonal claims that mainstream alignment research (interpretability, RLHF, scalable oversight, etc.) is fundamentally unable to produce alignment that scales to superintelligence, and is likely "net harmful when published" because it generates capability externalities. Instead, the only viable path is:

1. Design a fully formalized mathematical goal (QACI/ESP) such that an unbounded optimizer maximizing it would take actions humans consider desirable.
2. Build a new AI system from scratch that pursues this goal -- not retrofit alignment onto existing AI.
3. Launch this system as a "one-shot singleton" that takes over and steers the world toward good outcomes.

The causal chain: Orthogonal formalizes QACI/ESP --> independent or AI-assisted implementation of a QACI-aligned optimizer --> that optimizer achieves decisive strategic advantage --> utopia (or at least, a meaningfully increased fraction of surviving timelines).

Revealed Theory of Change

The gap between stated theory and revealed behavior is wide:

Stated: Orthogonal is an organization with multiple researchers doing urgent, world-saving work. Revealed: Orthogonal is effectively a solo project by Tamsin Leake, producing approximately one substantive post every 3-4 months (plus unlisted work of unknown scope), with no publications in 19+ months.

Stated: QACI is "our best shot" at saving the world, requiring urgent progress. Revealed: The research program has shifted from QACI to ESP (which Tamsin describes as superseding QACI2), and then appeared to halt entirely. Recent comments advocate donating to PauseAI, suggesting a possible update toward "buy time" strategies over "solve alignment."

Stated: Collaboration with MIRI is a priority. Revealed: No evidence of any MIRI engagement. No endorsement from any established alignment researcher.

Stated: Exfohazard caution motivates unlisting posts. Revealed: This policy may also serve to shield the work from the kind of external criticism that could reveal fundamental problems. The posts that ARE public have received very limited engagement.

The most charitable reading is that significant work continues in private (Discord, unlisted posts). The least charitable reading is that the project has stalled due to a combination of funding constraints, team-building failure, and possible recognition that QACI's foundational problems are not easily resolvable.

Key Assumptions

Assumption 1: Agent foundations are the right framing for alignment.

• Evidence for: Eliezer Yudkowsky and some MIRI-adjacent researchers believe current AI paradigms cannot be made safe; a "clean target" is needed. Orthogonal's pre-founding argument (027-gw-agent-foundations-needed.md) makes a detailed case.
• Evidence against: The broader alignment community has largely moved toward empirical/prosaic approaches. MIRI's own leadership stopped pursuing technical alignment agendas by 2023. davidad/OAA represents an alternative formal approach with more institutional backing (ARIA). The field's most impactful safety work to date has been prosaic (RLHF, constitutional AI, evaluations).
• Testable?: Only in the sense that if prosaic alignment proves sufficient, agent foundations were unnecessary. If prosaic alignment fails catastrophically, it will be too late to test.
• If wrong: Orthogonal's entire research program is misdirected, and the claimed "net harm" of prosaic alignment work is itself net harmful (by discouraging useful work).

Assumption 2: QACI's mathematical formalization is correct and meaningful.

• Evidence for: The QACI paper is unusually detailed for an alignment proposal; the mathematical specification is genuine, not hand-waving.
• Evidence against: The founder self-describes as "bad at math." No independent mathematician has verified the formalization. The ESP pivot suggests QACI had unresolved problems. The blob location problem (mapping mathematical bitstrings to physical reality) remains open. External critics say it is "speculative and hard to parse" with failure modes similar to HCH.
• Testable?: In principle, the math can be checked. In practice, the unlisted posts and custom notation make independent verification difficult.
• If wrong: The core technical output is flawed, and years of work on QACI were wasted.

Assumption 3: A one-shot singleton is the most likely and best AI outcome.

• Evidence for: Standard MIRI-style arguments about decisive strategic advantage and convergent instrumental goals.
• Evidence against: Current AI development is multipolar and distributed. No single actor controls enough resources for a singleton. Slow takeoff scenarios (which many researchers now favor) make one-shot approaches less relevant.
• If wrong: Orthogonal's entire framework (design a goal for a single all-powerful AI) is solving the wrong problem.

Assumption 4: A team of 1 person with $30K can make meaningful progress on the hardest problem in alignment.

• Evidence for: Some of the most important alignment ideas have come from individual thinkers (Yudkowsky, Christiano). Small teams can move fast.
• Evidence against: MIRI spent $20M+ over 15+ years with a much larger team and openly acknowledged failure to solve agent foundations. The mathematical difficulty of formalizing a complete alignment target is enormous. The lack of collaborators means no one is checking the work.
• If wrong: Orthogonal's underfunding is not a constraint to be worked around but a fundamental blocker.

Strengths

1. Intellectual honesty about the difficulty: Tamsin is upfront about high P(doom) and low success probability. There is no salesmanship or hype.
2. Genuine mathematical formalization: QACI is one of very few alignment proposals that actually specifies a formal goal in mathematical detail rather than gesturing at concepts. This is valuable regardless of whether QACI itself is correct.
3. No incentive misalignment: Zero lab funding, zero corporate ties. Orthogonal cannot be accused of pulling its punches to protect a funder's business model.
4. Philosophical clarity: The "backchaining" approach and rejection of prosaic alignment is clearly reasoned, even if one disagrees.
5. Research evolution: The QACI-to-ESP pivot suggests genuine intellectual progress, not dogmatic attachment to a single idea.

Weaknesses and Risks

1. Near-total lack of external validation: No established alignment researcher has endorsed QACI. No MIRI collaboration materialized. No Refine evaluator has commented publicly. No major funder has provided follow-on support. This is the most damning pattern.
2. Team failure: The "several promising researchers" never appeared. The fellowship never launched. Three years in, this is still a solo project. Agent foundations problems are extremely hard -- MIRI's team of 10+ couldn't solve them. Expecting one person to succeed where MIRI failed is unrealistic.
3. Publication gap: 19+ months without publication, in an org that claims short timelines make urgency paramount, suggests either the project has stalled or the research has hit a wall.
4. Self-sealing epistemology: The combination of (a) claiming most alignment work is "net harmful," (b) unlisting posts for exfohazard reasons, and (c) operating in a small Discord creates a bubble resistant to correction. If the approach is fundamentally flawed, there is no external mechanism to surface that.
5. Mathematical rigor gap: The founder acknowledges being "bad at math" while pursuing an approach whose entire value proposition is mathematical rigor. The ESP paper is self-described as "pseudomath." This tension has not been resolved by recruiting mathematically stronger collaborators.
6. MIRI's precedent: MIRI pursued agent foundations for 15+ years with more funding, more people, and deeper mathematical talent, and their leadership eventually acknowledged they couldn't find a viable approach. Orthogonal does not adequately explain why QACI/ESP will succeed where MIRI's research program failed.

Cross-References

• MIRI: Orthogonal explicitly claims to share MIRI's worldview. MIRI's trajectory (15+ years of agent foundations work, eventual shift away from technical alignment) is the most relevant precedent. Orthogonal appears to be repeating MIRI's early approach at 1/100th the scale.
• davidad/Open Agency Architecture (OAA): Competing "formal alignment" approach with ARIA backing. OAA and QACI should be directly comparable but have not been compared. OAA has more institutional support and more mathematical collaborators.
• Conjecture: Historical connection through Refine incubator. Conjecture's own trajectory (pivots, departures, controversy) provides context for the post-incubator independent research path.
• PauseAI: Tamsin's recent advocacy for PauseAI funding suggests a possible strategic update -- if technical alignment timelines are too short, buying time through advocacy becomes higher-priority.

What Would Change This Assessment

• Evidence of ongoing substantial research output (even in private/Discord) would significantly update upward. If Tamsin has been producing QACI/ESP work that simply isn't public, the assessment of "stalled" would be wrong.
• An independent mathematician verifying and extending the QACI formalization would address the most serious technical concern.
• MIRI researchers publicly engaging with QACI (positively or critically) would break the pattern of community silence.
• A team of 2+ competent alignment researchers joining Orthogonal would address the "solo project" weakness.
• If prosaic alignment approaches demonstrably fail at scale (e.g., a serious alignment failure from a frontier lab), the case for agent foundations approaches like QACI would strengthen dramatically.
• If Tamsin publicly explains the publication gap -- whether research hit a wall, funding ran out, or priorities shifted -- this would allow a more accurate assessment.

Self-Critique

Weakest claim: My assessment that the project has "stalled" is based on public evidence only. If substantial work is happening in Discord or unlisted posts, this assessment could be significantly wrong. I have no visibility into the ~300-person Discord community.

Potential bias: I may be implicitly anchoring to the norm of "alignment orgs should publish frequently and visibly." Tamsin's exfohazard argument -- that secrecy is genuinely protective -- deserves more weight than I may be giving it. However, the absence of any update, even something as simple as "we're still working," over 19 months is hard to explain by exfohazard caution alone.

What a thoughtful disagreer would say: "You're evaluating a theoretical research project by the standards of a startup or policy org. Einstein published 4 papers in one year then was quiet for years. QACI-style work requires deep thinking, not quarterly output. The fact that nobody famous endorses it is exactly what you'd expect for a genuinely novel approach -- breakthroughs aren't born with consensus. And the criticism that QACI is 'speculative' is trivially true of every agent foundations approach, including ones you'd probably rate more favorably."

What I'd most want to know: Whether the Refine evaluators (Byrnes, Kosoy, Hubinger, et al.) have any private assessment of Tamsin's work. Their silence could mean "not worth commenting on" or "interesting but we haven't engaged enough to say."