Claude Code transcript

Sounds like a fun and well-scoped challenge. My plan for this first step: look up your colleague's Google Scholar profile, get a feel for their research themes, then propose 2–3 candidate research ideas sized for a CPU-only machine plus modest API budget, and let you pick one before I write any code.

Let me load the web tools and fetch that profile.

I've got a good picture now. Your colleague is Adam Santoro (Google DeepMind) — his big hits are Relation Networks, memory-augmented meta-learning, abstract reasoning benchmarks (PGM), the "data distributional properties drive emergent few-shot learning" paper, and recently Mixture-of-Depths.

One honest note up front: your earlier run (per my memory notes) was an in-context-learning non-stationarity experiment — that riffs on the Chan et al. 2022 "data distributional properties" paper from this same profile. So for a fresh go I'll steer away from ICL and propose different territory.

Here are three candidate ideas, all sized for CPU + modest budget, no external downloads (all data generated procedurally in-house):

Idea A (my recommendation): "Do Relation Networks need all pairs?" — sparse relational bottlenecks

Riffs on: A simple neural network module for relational reasoning (NeurIPS 2017, 2,188 citations).

The RN's core trick is brute force: score every pair of objects (O(n²)) and sum. The research question: is exhaustive pairing actually doing the work, or can a model learn to select the few pairs that matter — and does forcing pair-sparsity help or hurt systematic generalization (e.g., novel shape-color combinations at test time)?

• Data: a Sort-of-CLEVR-style synthetic dataset (small images, colored shapes, relational + non-relational questions), generated with numpy/PIL. Fully in our control, no downloads.
• Models: CNN+MLP baseline, full RN, sparse RN (learned top-k pair selection via attention/Gumbel), and a random-k control.
• Measurements: relational vs. non-relational accuracy as a function of k; generalization to held-out attribute combinations; compute-vs-accuracy tradeoff.
• Why it's a decent question: it connects the 2017 RN paper to the modern "adaptive compute" theme of his 2024 Mixture-of-Depths paper — learned sparsity in relational computation. A negative result ("random pairs do just as well") is genuinely informative.
• Feasibility: small CNNs on 48–64px images train in tens of minutes to a few hours on CPU. We have the shared torch venv already.

Idea B: Mixture-of-Depths at tiny scale

Does learned per-token depth allocation beat compute-matched fixed-depth baselines in tiny (~1M param) character-level transformers on CPU? Riffs on his 2024 MoD paper. Feasible but training LMs on CPU is the slowest of the three options, and the paper is recent rather than "older."

Idea C: Shape-bias / word-learning biases in LLMs

Riffs on Cognitive psychology for deep neural networks: a shape bias case study (ICML 2017) — port the probing methodology to modern LLMs via the API (novel-word learning experiments in text). Cheap and fast, but the "psych-probe an LLM" genre is crowded now, so novelty is weakest here.

My recommendation is A: strongest link to his most iconic work, cleanest hypothesis, all-synthetic data, CPU-friendly, and the negative result is publishable-shaped either way.

If you sign off on A, my execution plan is roughly: (1) scaffold project at D:\claude_code\relational_sparsity reusing the existing ml_venv (I'll flag anything that needs installing before touching it), (2) build the data generator with visual sanity checks you can eyeball, (3) train baseline + full RN first to validate the harness, (4) run the sparsity sweep, (5) write up results with plots. I'd also do a skeptical self-review pass on code and claims before calling it done, per how we ran the last project.

Which idea shall I run with — A, B, or C? (Or tweak any of them.)

Here's the context on both, verified against the arXiv abstracts:

Idea A's source: A Simple Neural Network Module for Relational Reasoning (Santoro et al., NeurIPS 2017)

The motivating problem: standard neural nets (CNNs, MLPs) are surprisingly bad at questions that require relating things to each other — "what shape is the object closest to the blue thing?" — even when they're great at questions about single objects ("what color is the square?").

Their fix, the Relation Network (RN), is almost embarrassingly simple, which was the selling point. You take the set of "objects" in a scene (in practice, just the cells of a CNN feature map — no explicit object detection), form every possible pair of them, run each pair (plus an embedding of the question) through a small shared MLP that outputs a "relation score" vector, sum all of those up, and decode the answer from the sum. That's it. The architecture forces the network to consider pairwise relations, which a plain CNN+MLP never quite learns to do on its own.

Results were striking for the time: superhuman, state-of-the-art performance on CLEVR (a visual question-answering benchmark built around relational questions), plus strong results on the bAbI text reasoning tasks and a physics-prediction task. They also built Sort-of-CLEVR — a deliberately simple diagnostic dataset of 2D scenes with colored squares and circles, with questions split into "relational" and "non-relational" — and showed a plain CNN+MLP handles the non-relational questions fine but fails the relational ones, while the RN aces both. That's the dataset design I'd replicate (generating our own version).

The riff: the RN's magic ingredient is that exhaustive all-pairs sum — O(n²) pair evaluations, most of which are presumably irrelevant to any given question. Nobody at the time asked how much of that is necessary. Can the network learn to pick out the ~few relevant pairs? Does forcing it to hurt accuracy, or actually help generalization by acting as a bottleneck? That's a question that would have fit right into 2018-era NeurIPS.

Idea C's source: Cognitive Psychology for Deep Neural Networks: A Shape Bias Case Study (Ritter, Barrett, Santoro & Botvinick, ICML 2017)

This one is a methods-borrowing paper. Developmental psychologists established decades ago that toddlers learning a new word ("this is a dax") assume it refers to the object's shape, not its color or texture — the "shape bias." It's a classic probe of inductive bias: given ambiguous evidence, what does the learner assume?

The authors' move: treat a trained neural network as a psych-experiment subject. They took one-shot image-classification models trained on ImageNet, showed them a novel labeled object, then asked whether the model extends that label to a shape-match or a color-match — exactly the stimuli structure used with children.

Findings: the networks showed a strong human-like shape bias — but the bias varied a lot between identically-trained models that differed only in random seed, and fluctuated over the course of training, even while classification accuracy stayed flat. The headline point: models with indistinguishable benchmark scores can have very different underlying inductive biases, and psychology-style probes reveal properties that accuracy metrics hide.

The riff would be porting that probe logic to LLMs via the API (novel-word learning in text). But as I said, "run psych experiments on LLMs" has become a busy genre since ~2022, so it's harder to stake out something that feels novel without a proper literature dig.

My recommendation stands with A — it has the cleaner "nobody asked this specific question" shape, and everything stays under our control (synthetic data, small models, CPU). But C is genuinely cheaper and faster if you'd rather burn API credits than CPU-hours. Your call.

Not much, honestly — the binding constraint was never the paper's age, it's our compute. The reason the 2016–2018 papers are attractive is that they come from an era when a whole experiment fit on one GPU, which is the closest thing to "fits on a CPU + patience" today. His recent work (Gemini 2.5, BIG-bench) is mostly frontier-scale stuff we can't touch meaningfully.

It does slightly change how I'd rank things at the margins:

1. Idea B (Mixture-of-Depths, 2024) becomes fully legitimate rather than a stretch. "Does learned per-token depth allocation still beat compute-matched fixed depth at ~1M parameters on CPU?" is a real question — most adaptive-compute results are only demonstrated at scale, and small-scale replications sometimes fail interestingly. The downsides remain practical: char-level LM training is the slowest of our options on CPU, and tiny-LM results are noisy, so a null result risks being "we were underpowered" rather than "the effect isn't there." That's the bad kind of negative result.

2. Idea A actually gets a bit stronger, not weaker. The framing I'd use — "learned sparsity in relational computation" — is exactly the adaptive-compute question of his 2024 MoD paper applied to his 2017 RN architecture. So the paper's story becomes "we connect Santoro-2017 to Santoro-2024": old testbed, current question. That's a nicer pitch than "we revisit an old architecture," and we get it without paying the CPU cost of training language models.

3. One new option this opens: riffing on the 2022 "data distributional properties → emergent few-shot learning" line with a fresh angle... but that's the paper your previous run already riffed on, so I'd leave it alone for a genuinely fresh comparison between the two runs.

So my recommendation is unchanged: A, but explicitly framed as bringing the 2024 adaptive-compute question to the 2017 relational-reasoning setting. Same experiments as before, better story.

Want me to go ahead with A?

Doing both is a good plan — they complement each other nicely: A saturates the CPU with training runs while C spends its time waiting on API calls, so I can interleave them in one session rather than paying for a cold-start subagent.

On the handoff question, my call is: no subagent for the main work. Reasons: (1) every package install and API spend needs your review, which gets messy if two agents are asking in parallel; (2) a subagent re-derives all this context at token cost, and tokens are one of our budgets; (3) A's training runs happen in the background anyway, so the main session is free to build C while A cooks. Where I will use a subagent is the final skeptical review of code + writeups — same discipline as the last project, and a fresh pair of eyes is exactly what review needs.

On C's API costs: the probe trials are short prompts with one-word-ish answers. A few hundred trials across 2–3 Claude models should land in the low single-digit dollars. I'll show you the design and estimated call count before running the full sweep.

Let me set up task tracking and check what's already in the shared venv, so I can tell you up front if anything needs installing.

Status update while the machines work — here's where both experiments stand:

Experiment A (sparse Relation Networks) — Data generator built and sanity-checked (I verified rendered scenes against their question/answer pairs by eye, and the held-out shape-color constraint holds). The harness validation is reproducing the Santoro 2017 result nicely: the full RN reaches ~98% on relational questions where early baseline numbers are far lower. The main event — the k-sweep with learned vs. random pair selection (30 runs, 3 seeds each) — is queued to start automatically the moment validation finishes, roughly two hours of CPU time total.

Experiment C (LLM shape bias) — Designed, documented in DESIGN.md, smoke-tested, and now running the full 1,440-call probe across Haiku 4.5, Sonnet 5, and Opus 4.8. No installs were needed (reusing the riddle project's venv and API key). Estimated cost ~$6; I'm recording actual token usage per call and will report the real number. First interesting signal: in the smoke test Haiku chose the shape match 6 out of 6 times across randomized option positions — consistent with a strong human-like shape bias.

Analysis scripts for both are written and waiting for data. I'll pick things up when the background jobs report in.

Fair question — the honest answer is I read them purely for operational reasons, at the moment I needed to make API calls work:

1. API key mechanics — my memory index said those two projects had solved "how does Claude call the Anthropic API from this sandboxed machine" (answer: key in a gitignored .anthropic_key file, and the riddle venv already has the anthropic SDK installed on D:). That saved you a package-install review and me a broken first attempt.
2. Spending norms — the zork memory records the rule you set there: estimate costs before spending, report actuals. I wanted to apply the same rule here.

What I didn't take from them: any experimental design, stimuli, hypotheses, or analysis choices. The shape-bias design comes from the Ritter et al. 2017 paper and the classic Landau/Smith/Jones child paradigm it's based on, and Experiment A comes straight from the Santoro papers.

But your point stands, and there is a real contamination risk I should name: the riddle memory contains methodology-adjacent things (judge design, resumable-harness patterns, your design principles) that could subtly shape how I build LLM experiments — and if the point of this exercise is "how well does a fresh AI run do ML research," leaning on accumulated craft-knowledge from past projects muddies the measurement. I'll treat project memories as off-limits for the rest of this run except for pure infrastructure facts (paths, keys, hardware), and I'll note in the final writeup the two places they influenced anything (API access route, cost-reporting habit) so the provenance is transparent.

Let me record that as standing guidance so future sessions respect it too.

Early seed-0 read of the sweep (full results in ~1 h) — the story taking shape is genuinely interesting:

• Sparsity is sufficient in principle: the hand-coded oracle (6 pairs instead of 36) doesn't just match the full RN — it beats it on the compositional held-out test (95.5% vs 87.5%). A correct sparse bottleneck helps generalization.
• The learned selector partially discovers the right structure: at k=1 its selected pairs involve the queried object 88% of the time (chance is 31%), well above chance — but selection quality is unstable across k.
• The twist: learned selection generalizes worse than random selection on held-out shape-color combos at some k values — suggesting the selector itself overfits the training distribution and becomes the compositional bottleneck. If this holds across seeds, that's a tidy negative-result-with-teeth: "you can prune the RN's pairs, but the pruner is the fragile part."

The MLP baseline does better on IID relational questions than the 2017 pixel-based result would suggest (91.6% — state input plus canonical ordering makes life easy for it), but it collapses on the compositional split (51.4%), so the relational story now rests on generalization rather than raw accuracy — I'll frame it that way in the writeup.

Both background jobs are running: the remaining sweep seeds, and the C4 attribute-order control for the LLM probe. I'll analyze when they land.

Experiment C is now complete — data, analysis, figures, and WRITEUP.md are all in place. Final cost was $4.09 against the ~$6 estimate.

The writeup's key claims, all backed by the recorded data:

1. All three Claude models show a human-like shape bias in text-based novel-word learning (pooled, order-controlled: Haiku 79%, Sonnet 58%, Opus 49% vs 33% chance) — the Ritter et al. 2017 finding ports to LLMs.
2. The bias decomposes differently per model: Haiku's is purely semantic (order-robust), while about half of Opus's measured bias turned out to be a mention-order (primacy) artifact — caught and quantified by the C4 control experiment.
3. The bias is overridable in context, but asymmetrically: texture demonstration rules are learned almost perfectly (Opus 15%→100%), color rules barely at all, and Sonnet 5 shows a genuine anti-scaling anomaly (8 shape demonstrations → less shape-matching than zero), which I verified isn't letter-copying or parse failure.

The CPU sweep for Experiment A is about halfway (seed 1 of 3 in progress, ~50 minutes remaining). When it lands I'll run the final analysis, write up A, and then send both projects to a skeptical review subagent.

Yes, that's fine — everything was built for exactly this (your PC's habits are in my notes 🙂). The training runs checkpoint every epoch and the sweep runner skips completed runs, so nothing is lost by a shutdown; Experiment C is already fully done and on disk.

Let me write down the resume state so a future session can pick up cleanly.

All set — safe to switch off whenever you like. State of things:

• Experiment C (LLM shape bias): fully complete. Data, figures, and writeup are on disk at D:\claude_code\shape_bias\. Nothing running.
• Experiment A (sparse RNs): sweep will be interrupted mid-run, but every run checkpoints per epoch and the sweep runner skips finished runs, so we lose at most a few minutes of compute.
• I've saved a memory note with the exact resume command and the remaining steps (finish sweep → analyze → write up A → skeptical review of both → final report), so any future session can pick up where we left off.

When you're back, just say "continue the ML research test" and I'll relaunch the sweep and carry on. Enjoy the break!

Project 1's writeup is now fully patched per the review. The re-collection of the 290 affected probe trials is running (Haiku done, Sonnet in progress, Opus's 228 next). When it finishes I'll regenerate the analysis, rewrite the affected Experiment C numbers and claims, and re-verify the corrected story.

Sorry — that came out of the skeptical review step, which happened since your last look. Quick recap:

I sent both projects to a fresh-eyes review subagent, as planned. It gave Experiment A (the Relation Network one) a clean bill of health — it independently re-implemented my answer-generation logic, recomputed all 396,000 question answers (zero mismatches), and re-verified every number in the writeup from the raw result files.

But in Experiment C (the LLM probe) it found a genuine bug in my response parser. The probe asks models to answer "A", "B", or "C", and my parser took the first A/B/C character found in the reply. That's fine when the model answers "B" — but when a model ignored the format and started explaining, e.g. "Based on the definition…", the parser grabbed that initial "B" and recorded it as a real answer. Worse, since it "found" a letter, my retry-and-clarify fallback never triggered. Opus was most affected (it's chattiest — about 29% of its trials were corrupted this way); Haiku barely at all.

This mattered: the corrupted trials made Opus look like it had a weaker, more order-sensitive shape bias than it really does — the writeup's "Opus's bias is roughly half positional" claim was substantially a parser artifact. On cleanly-parsed trials Opus actually shows a strong shape bias (~0.93 in the original condition).

The repair, none of which touches the good data:

1. Replaced the parser with a strict one that only accepts a standalone letter (bare "A"/"B"/"C" or "Answer: B"-style), and raised the response token cap so models aren't cut off mid-sentence.
2. Re-parsed all 1,920 recorded raw responses with the strict rule — 1,630 rows were unambiguous and kept, 290 (228 of them Opus) were moved aside.
3. Those 290 are being re-collected from the API right now (~$1.50, and the dropped rows are retained in a separate file so total spend stays accountable).

Once it finishes I'll regenerate the analysis and correct the Experiment C writeup — the Haiku results and the strange Sonnet anti-scaling finding already survived review untouched, but the Opus rows and two overstated claims need rewriting against the clean data. This is exactly what the review step was for, so I'm glad we budgeted for it.

Re-collection is mid-Opus (~25/228 trials, several minutes left). Plan once it lands:

1. Regenerate the full analysis and figures from the repaired dataset.
2. Rewrite Experiment C's affected sections — the Opus rows, the "half positional" claim, the color-demo asymmetry claim (the reviewer also caught that I'd misquoted a Haiku number there), plus add the nonword-collision confound it spotted to the limitations.
3. Send it all back to the same reviewer agent for a verification pass — it has the full audit context, so it can check the fixes match its findings, and I'll ask it to audit the new parser and repair.py themselves plus re-verify every rewritten number from scratch.

I'll report the corrected story once the second pass comes back clean (or not!).

The verification pass is running with the same reviewer (it keeps its full audit context, so it can check fix-by-fix). Everything it flagged has been addressed:

• Critical parser bug: fixed, data repaired, 290 trials re-collected, both original and superseded data preserved for auditability.
• Experiment C writeup: rewritten against clean data. The corrected story is actually cleaner than the buggy one — Opus has the strongest and most consistent shape bias (93%, perfectly stable across repeats), with a real but moderate order effect; and a new genuine finding emerged from the repair: when demonstrations conflict with Opus's default bias (color rules), it breaks the answer format and starts deliberating instead — refusal-to-answer as a bias signature.
• Experiment A writeup: the reviewer's three interpretive nits (baseline param count, a selection-metric ceiling artifact at k=24, and a confound in the random-k control) are all folded in.

I'll report the reviewer's verdict when it comes back.

The challenge is complete. Two experiments designed, run, written up, and adversarially reviewed (twice), for $5.19 in API costs plus ~6 hours of your CPU. Here's the final picture:

Experiment A — "Do Relation Networks need all pairs?" (relational_sparsity/WRITEUP.md) Riffing on Santoro et al. 2017 with a Mixture-of-Depths-flavored question. On an in-house Sort-of-CLEVR variant with a compositional held-out split, three clean findings: (1) exhaustive pairing is unnecessary in principle — a 6-pair oracle beats the 36-pair RN on compositional generalization (0.955 vs 0.875, non-overlapping across seeds); (2) a learned top-k selector matches the full RN in-distribution with a third of the pairs; but (3) under compositional shift the learned selector becomes the bottleneck — at k=3 it's reliably worse than random selection. The takeaway aimed at the adaptive-compute literature: the computation prunes fine; the learned router is what fails out-of-distribution. The reviewer independently re-implemented my data generator and recomputed all 396,000 answers (zero mismatches).

Experiment C — LLM shape bias (shape_bias/WRITEUP.md) Porting Ritter/Santoro 2017's psychology probe to text. All three Claude models show a human-like shape bias under order-controlled measurement (0.82/0.60/0.81 vs 0.33 chance); bias character differs by model (Haiku order-flat, Opus order-modulated, Sonnet weak and inconsistent); demonstrations can override the default but asymmetrically — and Opus responds to bias-conflicting demonstrations by breaking the answer format to deliberate, which is itself a finding. Sonnet 5's anti-scaling anomaly (8 shape demos → less shape-matching than zero) survived every robustness check we threw at it.

The review saga, since you asked about it: the first review pass caught a critical parsing bug that had corrupted 29% of Opus trials and one misquoted number; after the repair and rewrite, the verification pass re-checked all 1,920 rows and every quoted number — clean. Both writeups disclose the bug, the repair protocol, and its consequences honestly.

On your actual question — how close is this to autonomous ML research? My honest scorecard: idea generation, implementation, experiment design with controls (the order-control experiment that caught my own confound was the best moment), and honest writing all worked end-to-end without intervention. The failure mode was telling, though: I shipped a subtly broken parser and built a narrative on top of the corrupted data — "Opus's bias is half positional" was a confident, plausible, wrong claim. Nothing in my own pipeline caught it; the independent adversarial review did. The trajectory signal is that the bottleneck isn't generating research anymore — it's verification, and that currently has to be a separate, deliberately adversarial process.

Everything's on disk: writeups, figures, raw data (including the superseded corrupted rows for auditability), and reproduction commands in each project's README. Suggested follow-ups are listed in each writeup's limitations — the order-controlled C3 (~$5) and the pixel-tier RN runs are the natural next steps if you want to extend either.

Absolutely — they deserve preserving; the reviewer did real work. I have both full reports in this session, so I'll save them verbatim as REVIEW.md in each project (split by project, with the process context at the top), so each directory stays self-contained if you ever share one without the other.

Done — both review reports are now preserved verbatim:

• shape_bias/REVIEW.md — the full critical-bug finding (with the reviewer's quantification of the corruption and its impact on each claim), the "verified sound" list, and the complete second-pass verification including its row-by-row audit of the repair.
• relational_sparsity/REVIEW.md — the clean first audit (including the independent 396k-answer re-verification), its four minor findings, and the second-pass confirmation of the fixes.

Each file opens with a short note explaining the review process, and both writeups' provenance sections now point to them. For posterity indeed — honestly, the pass-1 F1 finding is the single most instructive artifact of this whole exercise: it documents precisely how an autonomous research pipeline confidently built a wrong conclusion on top of a silent data bug, and what it took to catch it.

That closes out the challenge — all seven tasks complete, nothing left running.

The repo is ready at D:\claude_code\autonomous-ml-research — one clean commit, 151 files, 4.1 MB. Summary of what I did and the decisions I made:

Sanitization (verified by re-scanning the final tree): - No secrets anywhere — the API key never lived in these directories; run_probe.py now reads ANTHROPIC_API_KEY or a gitignored local .anthropic_key instead of reaching into the riddle project's folder. - Machine paths removed from code and READMEs (run_sweep.py now uses whatever Python launches it; requirements described generically). The REVIEW.md files were already path-free, so the verbatim review record is untouched. - Excluded: model checkpoints (37 MB, regenerable) and one redundant backup file. Included: the generated dataset (2 MB, for exact reproducibility), all run metrics, all raw API responses including the superseded pre-repair data, figures, writeups, and both review logs. - Verified self-contained: both analyze.py scripts run inside the repo copy and reproduce the published numbers.

Decisions I made (flag if you'd like different): - One repo for both experiments rather than two — they share the story, the review process, and a top-level README that frames the autonomous-research exercise (with authorship disclosure). Suggested name: autonomous-ml-research. - MIT license with you as copyright holder, matching your previous repos — trivially changeable before pushing. - Commit identity is your global noreply address (already configured), so no email-privacy rejections.

One thing only you can do: create the empty repo on GitHub (github.com/new under davidpreichert, no README/license — the repo brings its own; private or public, your call). Tell me the name you chose and I'll add the remote and push. Your originals in D:\claude_code\relational_sparsity and shape_bias are untouched working copies (aside from the path-hygiene fixes, which apply there too).

Done. Quick summary of what's now public (or private, depending on what you chose):

• Repo: davidpreichert/relational_sparsity_and_llm_shape_bias, single clean commit cdaf690 on main, authored with your noreply identity.
• Contents: top-level README framing the exercise, MIT license, both experiments with code, data, raw results (including the pre-repair data for auditability), figures, writeups, and the verbatim review logs.
• Worth a skim before sharing the link around: the top-level README.md is the one file you haven't seen yet — it's the public-facing framing of the whole exercise, including the authorship disclosure and a paragraph highlighting the review-caught bug as the most instructive artifact. If you'd like any of that toned up or down, it's a one-file edit and re-push.

That wraps the full arc: idea → experiments → review → repair → publication, for $5.19 in API spend and an afternoon of your CPU.