LLM agents increasingly modify their own prompts, tools, middleware, resources, and execution harnesses at runtime. Such self-evolution can improve capability, but a successful mutation may leave persistent effects that cannot be safely reversed in states different from the one in which it was created.

We introduce EvoUndo, a framework for representing, synthesizing, diagnosing, and independently verifying recoverability of model-generated self-modifications across counterfactual states. Across 600 unseen one-shot self-evolution tasks, we identify 197 capability-improving mutations that fail recoverability verification. Under the original recovery representation, conventional repair strategies recover 0/197 of these natural failures. Deterministic oracle analysis recovers 48/197 under the original recovery language L0, while the extended recovery calculus increases empirical oracle recovery to 191/197.

A protocol-locked 2×2 grounding-by-expressivity intervention then separates two bottlenecks: exact state-address grounding increases successful recovery from 0/48 to 38/48 (79.2%) when the original language is sufficient, while extending the recovery language enables recovery on 142/143 (99.3%) failures in the oracle-defined S1 stratum.

On the primary gpt-oss-120b backbone, adding exact-address diagnostics to the richer language reduces recovery to 133/143 (93.0%); a Qwen3.8-27B replication preserves the grounding and expressivity effects but not this negative interaction, indicating that the latter is model-dependent.

These results indicate that reliable agent self-evolution requires co-designing verification, state grounding, witness semantics, and recovery-language expressivity rather than relying on iterative prompting alone.

Paper: https://arxiv.org/abs/2608.28363

Hi everyone,

2nd-year PhD candidate here staring down my first A* submission deadline (AAMAS 2027). I could really use some perspective on theory expectations, especially since I think I’ve methodologically painted myself into a corner.

The setup

My project started with a clean hypothesis: if architecture X is more robust than Y to perturbation A, and B is a strictly harder version of A, then the X > Y ordering should hold under B as well. I isolated three variables I suspected were driving the effect, ran experiments, and… got results that only partially support the hypothesis, with clear boundary conditions.

Where I got stuck

Trying to explain the “why” mathematically sent me down a theory rabbit hole. I ended up with two bad options:

1. Claims tied to specific training outputs rather than structural/architectural properties, or
2. Weak, hand-wavy speculations that feel like post-hoc rationalizations.

I’m pretty sure I fell into HARKing.. I started building theory after seeing the results instead of deriving predictions beforehand.

Furthermore, my codebase is built on an undocumented public repo, and I recently found a bunch of hidden parameters set to wrong values for my setting. I’m currently re-running everything, which is why I’m being vague about specifics. My “insights” from the first round are probably garbage.

My actual questions

• For those who’ve reviewed for or published at AAMAS (or similar A* venues): how much formal theory is actually expected for an empirical MARL paper? Is “here’s the phenomenon, here’s the controlled experiments, here’s a plausible but incomplete theoretical sketch” a death sentence?
• If the theory ends up being training-dependent rather than structural, is that a sign I should pivot to a lower-tier venue, or can strong empirical characterization + limited theory still fly at A*?
• How do you recover from HARKing mid-project when you’re under pressure to publish in year 3/4 of a 4-year contract?

Any advice on how to salvage the timeline or reframe the narrative would be hugely appreciated.

YOLO26 ships a depth-estimation model — dense, full-resolution, per-pixel regression, a task architecturally much closer to image restoration than to detection. I wanted to know whether the backbone+neck weights it learns through depth training transfer to a different dense-regression task (deraining), compared with training the same architecture from scratch. The deraining model that came out of it is a useful byproduct, but the transfer result is the part I think is worth discussing.

What I inherited from YOLO26-depth

• The CSPDarknet backbone and PAN-FPN neck, unchanged.
• The depth decoder's multi-scale fusion (project the P3/P4/P5 pyramid to a common width, progressively upsample-and-add P5→P4→P3). That part isn't depth-specific — it's just feature fusion — so RGBHead reuses it.

What I changed / added

• Replaced the 1-channel Depth head with a new RGBHead. The config change is one line; RGBHead itself is a new restoration decoder, not a re-pointed depth head.
• Reconstruction tail that continues to full input resolution (deraining needs pixel-exact output; depth stops at 1/4 res).
• Skip connections from the stride-2 and stride-4 backbone layers into the tail, so fine detail has a path that doesn't route through an 8×-downsampled bottleneck.
• Residual output — the head predicts a correction added to the input (NAFNet/Restormer-style), not the image directly.
• LayerNorm in the head's own conv blocks; the backbone and neck stay on BatchNorm (folds into conv at TensorRT export, and keeps the model loadable from the whole YOLO26 pretrained zoo, not just the depth checkpoint).

How it was trained and measured

ClearView as an external lib — its mixed synthetic+real rain recipe, Charbonnier loss, and 10-test-set protocol — so the numbers land on ClearView's own model-zoo scale, not a benchmark I made up. Released scales: nano (5.25M) and small (12.13M).

Loading the YOLO26-depth checkpoint into this architecture matches 468/468 backbone+neck tensors exactly — only the new RGBHead is randomly initialized. So the controlled comparison is: identical architecture and recipe, backbone+neck either from the depth checkpoint or from scratch.

The transfer result (the interesting bit)

A controlled initialization experiment at nano scale — same architecture, same recipe, fixed 100 epochs each — backbone+neck from the YOLO26-depth checkpoint vs. random init:

Deltas are from the unrounded averages (27.935 vs 27.452 PSNR). Small, but the depth init wins on every one of the 10 test sets.

(These are 10-set averages, AllWeather included, from the 100-epoch controlled run — so they're lower and not directly comparable to the 9-rain-only released-model numbers in the ranking table below, which come from longer training.)

On "did the random model just need longer to converge?" — both conditions ran a fixed 100 epochs, and the gap isn't a convergence-speed artifact: a 1-epoch check was a statistical wash, by 20 epochs the gap was already ~+0.49 dB, and at 100 epochs it was +0.48. It appeared early and didn't close with more training.

This does not establish why — whether depth supervision teaches geometry/spatial structure that's useful for restoration, or whether YOLO26-depth just happens to be a strong pretrained checkpoint. Only that, in this setup, the depth-initialized representation is a better starting point than random. Per-dataset deltas are in the repo; happy to paste them in a comment.

Accuracy (avg PSNR over 9 rain-only test sets, ClearView's ranking convention):

ClearView's own analysis points to the classification stem's early downsampling (a stride-4 entry before any residual block runs) as a likely reason the ResNet-UNet baselines underperform. This project doesn't test that directly — the ResNet-UNet comparison is a whole-architecture comparison, not a pretraining ablation — but it's the context the depth-vs-random experiment sits in.

Note NAFNet-Small (1.1M, 31.15 dB): smaller and higher PSNR than yolo26_rgb_n, but ~4× slower (26.9 qps). So this isn't Pareto-dominant on every axis — the story is specifically the real-time / YOLO-derived operating point, not "more efficient in every sense."

Deployment (TensorRT fp16, 1920×1080, batch 1, RTX 4070 SUPER 12GB; baseline figures are ClearView's own on the same GPU/TRT version)

The clean pairwise comparisons against the ResNet-UNet family:

• yolo26_rgb_s — 12.13M, 30.95 dB, 92.2 qps vs ResNet34-UNet — 24.5M, 30.45 dB, 94.9 qps → same speed, ~half the params, +0.5 dB
• yolo26_rgb_n — 5.25M, 30.83 dB, 108.6 qps vs ResNet18-UNet — 14.4M, 30.23 dB, 110.3 qps → same throughput, ~1/3 the params, +0.6 dB
• Both are ~3× faster than ResNet50-UNet (73.3M, 30.63 dB, 33.1 qps), while also scoring higher PSNR.
• Restormer (rank 1 on PSNR) doesn't build under TensorRT at 1080p on this 12GB card in my setup — TensorRT reports ~14.4GB of scratch needed to fuse its attention path.

What this shows — and what it doesn't

• Demonstrated: YOLO26-depth initialization beats random init for deraining in this setup (10/10 test sets, +0.48 dB), same architecture and recipe.
• Supported: the trained models sit at an attractive real-time quality/latency point relative to the ResNet-UNet baselines.
• Not demonstrated: that depth pretraining beats classification pretraining for restoration, or why depth helps. Those need experiments I haven't run.

Practical limitations: deraining is partial (faint streaks survive up close; dense rain over flat, low-texture backgrounds is the worst case). AllWeather (rain+fog) is out of domain — both YOLO26-RGB models and every ClearView baseline land around 13.5 dB, so it's excluded from the ranking. One task, two scales — not a general restoration model.

Solo side project. AGPL-3.0 (inherited from Ultralytics' YOLO26 license). Not affiliated with Ultralytics.

• Code: https://github.com/dronefreak/yolo26-rgb
• Models: https://huggingface.co/dronefreak/yolo26-rgb-n · https://huggingface.co/dronefreak/yolo26-rgb-s

Happy to answer questions on the architecture or the eval setup.

After following various arXiv papers and researcher discussions on X/bluesky about latent reasoning and continual learning, one idea which resonates strongly is that path forward (towards AGI) may depend less on generating ever-longer chains of thought and more on finding architectures that can reason beyond the token stream.

LLMs routinely reach correct answers through flawed or fabricated CoT steps, and produce perfectly logical steps that end in wrong answers (Kambhampati, 2025). The trace doesn't track the computation which clarifies that verbalized CoT is an imitation of reasoning and not the mechanism itself.

The alternative mechanism which gets the most attention is latent reasoning: instead of verbalizing every intermediate result, the model repeatedly transforms its continuous hidden state and decodes only the answer. 

I’m breaking latent reasoning down into at least five distinct families:

1. Continuous thoughts in autoregressive LMs: Coconut (Hao et al., 2024) feeds the model's own final hidden state back in as the next input embedding while Soft Thinking (Zhang et al., 2025) reasons in a continuous concept space. Theory here argues a single continuous state can hold several search frontiers at once and expand them in parallel (Zhu et al., 2025) .
2. Compressed discrete non-linguistic tokens: Abstract-CoT (Ramji et al., 2026) swaps verbal rationales for a short sequence from a learned vocabulary. It is non-linguistic, but still serial and externally decoded, the discrete end of the spectrum .
3. Recurrent depth and looped models: recurrent-depth LMs (Geiping et al., 2025) and looped Transformers (Saunshi et al., 2025; Zhu et al., 2026) reapply a shared block to a latent state. Mostly framed as parameter efficiency and test-time-compute scaling, not as a new reasoning interface .
4. Task-trained recursive solvers: HRM (Wang et al., 2025) and TRM (Jolicoeur-Martineau, 2025) recursively refine latent and candidate-answer states. Their ARC pipelines are transductive: evaluation-task demonstrations get augmented into optimization with learned per-puzzle identities, so an unseen task needs a backward pass before it can be answered .
5. In-context recurrent latent solvers: this is where BDH-CQ (Engdahl et al., 2026) sits, built on the Dragon hatchling architecture (Kosowski et al., 2025). Demonstrations write directly into a recurrent memory at inference time, and  new test inputs are then solved by iterative computation in a separate continuous latent space. The authors report a point beyond the previously published cost–accuracy Pareto frontier on public ARC-AGI-1, as well as early pretraining experiments show transformer-like scaling laws upto 600B parameters while preserving the latent reasoning behavior.

Two distinctions seem especially important: how a system acquires a new task (through context, memory, or gradient-based optimization or finetuning) and where its intermediate computation happens (through language tokens, abstract tokens, or continuous latent states)

Lmk if I have missed any family or papers. More importantly, if latent reasoning wins on efficiency, what happens to the readable traces on which much of industry's interpretability and evaluation work currently depends? Was CoT legibility a temporary consequence of how we scaled LLMs or is it a safety property worth paying an efficiency penalty to keep?

Hey everyone,

My brother and I just released TontaubeV1, a 2.9B-parameter open-weight TTS model focused on expressive speech, long-form generation/narration, and low-latency local inference. It is primarily aimed at English and German and supports zero-shot voice cloning from up to one minute of reference audio. It builds on DualCodec, a multi-codebook discrete audio codec. It was trained on 7 languages and ~200k hours of audio (mostly tested in English and German).

I wanted to make a post to highlight two choices that worked well for us and seem less common in current TTS models:

1. Character-level tokenization

We start from a Qwen3-1.7B checkpoint for our semantic codebook model. Many modern, and especially LLM-based, TTS models use the tokenizer from the backbone model, add special/audio tokens, and train the model on predicting the next token. We experimented early on with character-level tokenization and found that it generally worked better than using the original BPE tokenizer from Qwen.

We still use the tokens emitted by the Qwen tokenizer, but force it to tokenize spoken text as a sequence of individual characters. When experimenting with forcing Qwen to predict text in this mode, we found that it was still able to answer questions correctly, which suggested to us that language understanding was retained even with this unusual representation.

We did this because a) context length usually is not as much of an issue for TTS as it is for regular LLMs, since we do not require huge reasoning budgets and use chunking, and b) it makes the character-to-sound mapping much simpler internally. Speech is a lot about syllables and short character sequences.

When using the regular BPE tokenizer, we found that the model went out of distribution more often and was more likely to encounter a sequence of tokens that was rare or absent from the TTS training data. Complex sequences of special characters can be particularly confusing because they may tokenize into combinations that the TTS model has barely seen. This is amplified by the fact that TTS training covers far fewer text-token combinations than the full pretraining of an LLM.

2. Chunking and position scheme

The important part here is not just that we split long text into chunks. The chunk boundaries are part of the token layout and position scheme used during training.

The model processes several rows in one flat sequence: text, semantic audio, and the completed lower acoustic codebooks. If we simply used normal sequential position IDs, tokens representing the same moment in the audio would end up far apart because the rows are serialized one after another. Instead, the physical sequence order determines which tokens the model can see, while we assign separate logical position IDs. Codec tokens for the same audio frame share a position across codebooks, and text and audio are placed on the same approximate timeline.

Text advances by one position per character, while audio advances at 12.5 frames per second. These rates are fairly close for normal speech, but not identical, so the two streams usually need slight realignment after every chunk. We use paired text and audio split markers that share the same position. We also reserve an additional 25 character positions at each boundary. This prevents the generated audio positions from leaking into the next chunk’s text positions, while keeping the position IDs monotonic and approximately linear across the passage.

For every chunk, the semantic model sees the previous text and audio chunk, the current text, and a short lookahead into the next text. Once a chunk is finished, the oldest text-audio pair is discarded and the window moves forward. This keeps the model context bounded even for very long passages, while still retaining nearby text and audio context. The higher acoustic codebook models work on one chunk at a time and do not carry acoustic state between chunks.

DualCodec’s decoder is forward-looking, which makes directly decoding and joining separate chunks problematic. For streaming, we therefore decode overlapping DualCodec windows, re-encode them into the VibeVoice acoustic space, keep the stable middle sections, and decode them with a shared causal VibeVoice decoder state. This reduces audible seams between chunks and lets us emit audio before the full passage has been generated.

Here is figure 1 from our technical report:

The current release requires a GPU with at least 24 GB of VRAM for the low-VRAM and balanced profiles, or 32 GB for the high-throughput profile. A substantial part of the current VRAM requirement comes from vLLM’s KV-cache reservation and our multi-engine serving setup, which are designed for high concurrency and low latency. We plan to release quantized versions aimed at much smaller memory capacities and on-device use, as well as fine-tuning support.

We also ran a 400-passage LLM-as-a-judge audiobook benchmark. On prosody, TontaubeV1 scored 50.1% against ElevenLabs Flash v2.5 and was preferred over Fish Audio S2 Pro, Gradium, and Cartesia Sonic 3. The methodology, caveats, and confidence intervals are described in the report.

Human listening tests remain the gold standard, so take these results with a grain of salt. We were not able to conduct a large-scale human study before release, but we plan to submit TontaubeV1 to TTS Arena V2 and the Artificial Analysis Text to Speech Arena.

Links:

- HF model page: https://huggingface.co/TontaubeAI/TontaubeV1

- HF demo: https://huggingface.co/spaces/TontaubeAI/tontaube-v1-tts-demo

- Inference code: https://github.com/craitech/tontaube

- Technical report: https://tontaube.ai/papers/tontaube-v1-technical-report.pdf

Let me know if you have any questions!

I'm exploring Hidden Markov Models (HMMs) as a baseline method for "dataset exploration/discovery" where I have a bunch of unstructured data with no annotations, and wish to gain insights about the structure and semantics of the data within. I was wondering if there are more modern (deep learning based or otherwise) approaches which have completely superseded HMMs for such tasks.

I have submitted a paper to acml 2026 journal track, the official date of release of review is 27 August, but I have not heard anything from them, if anyone received the review then let me know I will write to program chairs.

Thanks

Sliding Window Attention with sinks, one of the simplest existing fixes for the quadratic-cost problem in LLMs, holds up as well or better than the linear-attention variants labs have been spending post-training compute to produce. That is the claim of a [new arXiv preprint](https://arxiv.org/abs/2608.28444) by Alexia Jolicoeur-Martineau, Rhea Sanjay Sukthanker, Pashmina Cameron and Emy Gervais.

On the long-context reasoning benchmarks the paper singles out, the gap is not close. "SWA achieves massively higher performance (2 to 10 times higher than linear attention)," the abstract reports, naming Needle-in-a-Haystack and BABILong as the two tasks.

The pitch is that the whole post-training-to-linear pipeline has been benchmarked against the wrong thing. "This line of research has not been properly compared to simpler baselines," the authors write. Their alternative needs no post-training, runs fast, and holds memory low.

The recommendation is blunt: "we strongly recommend switching to SWA instead of post-training linear models." Linear attention, the abstract concedes, "may have shown some promise, but they likely require to be trained from scratch or extensive post-training in order to even match SWA."

---

This is the time of year when the number of cold emails I receive about PhD positions tends to ramp up quite a bit. In many countries, this cold emailing is essentially part of the normal recruitment process, so there is nothing inherently wrong with doing this. However, there are a few things you definitely shouldn't be doing:

• Massive emails. The probability of me reading your email is inversely proportional to its length.
• Emailing everyone. Find supervisors that work in areas you are actually interested in. I do relatively foundational ML research (i.e., not associated with a specific application domain), but the majority of emails I get from prospective students are essentially "I want to apply ML to domain X". In many cases this does not constitute an ML research direction; you'd be better off finding a supervisor with expertise in domain X, which is where most of the impact will be.
• Generic research interests. If the most specific research interests you can give are "Machine Learning, LLMs, and AI" then I assume you only have a surface-level familiarity with the field, and are not ready for a PhD.
• Passing off workshop papers as conference papers. This has become a much more common thing in the last couple of years. It's a big red flag; I am not going to take on someone who is dishonest.
• Excessive AI use. Using them for fixing up grammar is fine, but if you outsource your thinking to LLMs then your research direction will be the same as everyone else who outsources their thinking to LLMs. This tends to result in something that would be an okay bachelor's thesis project, but nothing more than that. I get a lot of LLM emails, so determining if you are in this cluster is very easy.
• Summarise my paper. I already know what's in it, I don't need a summary. I care more about how you think you could build on it, or do something related. Don't use LLMs for this; see above point.
• Ignoring instructions on my website. Check prospective supervisors' websites for how you should be getting in contact with them. Often they will ask you to include something in the subject line to make sure your email goes to the right place. Ignoring this will send you straight to spam.

I'm sharing this new tabular data diagnostic tool (Entropic Scree). It can be used to estimate these properties of your high-d, real-world, dirty dataset:

• The informational volume of the signal (i.e., helps you assess whether the signal is strong enough to survive the dataset's idiosyncratic volume).
• The overall signal-to-idiosyncratic volume ratio (SNR).
• The intrinsic rank.
• Provides an exploratory map that allows for the identification of decoupled sub-networks of variables.
• The linear sufficiency (i.e., does the dataset align with the linear assumptions of standard PCA?).

Instead of evaluating linear variance, rank order, or Euclidean distance like traditional PCA variants, this new method evaluates a transformed mutual information metric. Relative to these baselines, it is less reliant on strong parametric or distance assumptions, making it appropriate to apply more broadly.

It also serves as a practical diagnostic of the theory explored in the From Garbage to Gold framework, which describes when and why uncurated, error-prone data can be used directly to create accurate prediction models.

There is a preprint that presents the full technical details, and Python and R packages will be released soon. Right now though, the original function is already available in R (see Quick Start R Function Code below).

• Entropic Scree Preprint: https://doi.org/10.5281/zenodo.22028087
• Entropic Scree GitHub: https://github.com/tjleestjohn/entropic-scree
• From Garbage to Gold Preprint: https://arxiv.org/abs/2603.12288

Let me know how it goes if you give it a try... or if you have any questions or comments of course.

############ 
# Quick Start R Function Code.
# To load the function, copy and paste the following into your R console, then hit enter. 
############

# 1. Define the direct URL to the raw function script on GitHub
url <- "https://raw.githubusercontent.com/tjleestjohn/entropic-scree/main/Entropic.Scree.v1.0.0%20-%20ENLI.R"

# 2. Define what you want to name the file on your computer
file_name <- "Entropic.Scree.v1.0.0 - ENLI.R"

# 3. Download the script to your current working directory
download.file(url, destfile = file_name)

# 4. Source the core function into your R environment
source(file_name)

# 5. Ex. To run the function and extract bipolar modules:
# results <- Entropic.Scree(dt 
#                         , extract_bipolar_modules = TRUE)
#
# View the extracted structural sub-networks for the primary axes:
# results$bipolar_modules

Hi, I'm making posters for ECCV 2026.

Does anyone have any ML/CV posters they thought were really well done?

Would love to see some cool examples.
Thanks

Third-year PhD student, NLP / interpretability. I want a reality check from people doing similar work.

I started using Claude Code for the boring parts: argparse boilerplate, plotting, config wrangling. Over the last few months the scope has crept. It now writes most of my experiment scaffolding, refactors my dataloaders, does first-pass debugging on training runs, and drafts the analysis scripts. I mostly read diffs and say yes.

The output is fine. My throughput is up. The thing bothering me is that I no longer hold my own codebase in my head. When a result looks off, I used to have an instinct about which line was lying to me. Now I go hunting like it’s someone else’s repo. I catch bugs later than I used to, and I catch them by reasoning about the numbers rather than by knowing the code.

I don’t think the tool is the problem. I think I delegated a layer that was doing more for my understanding than I gave it credit for.

Questions for people further along or in the same spot:

1. Roughly what fraction of your research code do you write yourself now?

2. Is there anything you deliberately refuse to hand off? (For me I think the eval harness and anything defining a metric should stay mine, but I keep breaking my own rule.)

3. Does anyone have a workflow that keeps the speedup without the detachment? Reading the diff line by line is not cutting it.

Not looking for a “tools are just tools” answer. I’m asking about the specific feeling of not owning your own experiments anymore.

I found this GitHub link, and the HTML file contains ~7k papers. Some are anonymized, and the details seem pretty accurate. It looks like these might actually be the accepted papers.

https://github.com/xll0328/NIPS26-

Can someone confirm whether this list is legit? I’m hoping it’s just a coincidence since it seems way too early.

Working on a pipeline that recovers a patient specific 3D distal femur from two orthogonal X-ray views (PA + lateral). No CT, no neural network, no massive training set.

approach: build a PCA shape model from 50 CT-derived femur meshes (MedShapeNet), then fit it to two silhouettes using PyTorch3D's soft rasterizer with sigma annealing. 10 shape coefficients, Mahalanobis prior to keep things plausible, Adam optimizer, ~1000 iterations.

The part that took the longest (and made me suffer the most too) : correspondence. Tried KD-tree nearest neighbor (50.7x roughness vs CT surface), CPD (28.2x), BCPD (47.5x), and FilterReg (couldn't even run). Finally got ShapeWorks working at 3.3x. only method that passed the 5x acceptance gate I set before testing.

LOO validation on 5 held out femurs: 0.86-1.43mm on within range targets. Two extreme cases failed because they sat outside the 49-mesh model's coverage on mode 1, the optimizer can't recover a coefficient the model doesn't support. Bridge ICP alignment was also poor on those cases (0.6 inlier fraction), which accounted for more error than the shape fitting itself.

Interesting finding: the sigma anneal endpoint has to match the reference render's sigma exactly. Hardcoding a constant tuned on one SSM caused an 87x accuracy degradation on another. Tying it to camera_extent × 1e-4 fixed it.

Still working on real X-ray validation (need paired CT data) and automatic segmentation. Happy to answer questions

Abstract:

We study autonomous mathematical discovery in the Station, an open-world multi-agent environment in which AI agents from different model families pursue a shared research goal without a central coordinator or scripted pipeline. Agents choose their own research directions, conduct experiments, collaborate, and build a shared scientific literature.

Across 12 construction problems from the AlphaEvolve catalogue and two additional case studies, the Station obtained results novel relative to the prior literature on five problems: a new infinite family of finite-field Kakeya sets, new exact 604-point kissing configurations in dimension 11, new records for the discretized Kakeya needle and sign uncertainty problems, and a substantially improved lower bound for Erdős's minimum-overlap problem.

Agents also discovered novel infinite families for Book Ramsey numbers. Importantly, the agents produced not only numerical constructions but also theorems and analyses explaining how those constructions work, making the results more interpretable and easier for mathematicians to build upon. We release all raw agent dialogues, proofs, and verification code, providing a transparent record of how these discoveries emerged.

Expecting a rejection from NeurIPS given our scores of 5/2/2. Trying to decide between ARR vs. TMLR, but thinking NAACL findings are more likely than main conference. Would you rather have TMLR or *ACL findings on your publication list? Genuinely curious to hear what people have to say.

Hey Guys,

I built a small open-source tool that checks whether a RAG application retrieves documents a user shouldn’t have access to.

It supports offline test cases and live HTTP API testing with bearer token/API-key auth.

I’m looking for a few engineers to try it on a test or non-sensitive environment and tell me whether it catches anything useful or what would make it better.

GitHub: https://github.com/InfraGuard-Labs/rag-access-check

Hello all, here is a chill post.

When I was an undergrad, I really liked working things out on a whiteboard. Drawing stuff, talking through ideas out loud, testing little hypotheses.

Now I work in radar DSP, and a lot of my work is code, numerical experiments, deep learning and waiting for training to finish 😅

I’m wondering how other people bring that whiteboard style of thinking into DSP, data science or ML work.

Do you still use a whiteboard regularly, or do you mostly go straight from idea to code?

Time Series Anomaly Detection (TSAD) seems to be one of the hottest topics in NeurIPS, SIGKDD, VLDB etc.

Many (perhaps most) papers evaluate on Paparrizos’ TSB-AD-M benchmark…

However, I tested these benchmark datasets and found that in most cases I could beat the SOTA TSAD methods with a 100-year-old algorithm, simple Statistical Process Control (SPC). In the attached example, SPC gets perfect results.

If we can beat the SOTA papers with 100-year-old algorithm, we probably should not be too impressed with them [b]. I really think this calls for some introspection by the community.

To be clear, I make no claims (here) about the proposed algorithms in all these paper. But the TSB-AD benchmark is obviously too trivial to make meaningful claims on [a][b].

The example shown is one of the ECG traces but look at dozen of traces marked “TAO”, they are even more trivial to solve with SPC [a][c].

I do not claim to have solved the triviality problem, but I have done 90% of the work to introduce more challenging TSAD problems ([d] sled dogs, [e] Tuna, Fuel Cells, Smart Manufacturing  etc.).

TLDR: I think the TSAD community needs more introspection on benchmarks. Most progress over the last decade seems to be illusionary.  

[a] https://www.youtube.com/watch?v=VftCMSI3C_s

[b] https://www.dropbox.com/scl/fi/31zuyhejb6sdjrom20frn/Problems-with-Time-Series-Anomaly-Detection.pptx?rlkey=mvcj1wz5s45kgazezopnih2h7&dl=0

[c] https://www.dropbox.com/scl/fi/42fkf9q9hft2224dnm83v/The-TSB-AD-Benchmarks-are-Nonsense.pptx?rlkey=5fwjopie5ncjhkgr0wqhdm2lp&dl=0

[d] https://www.linkedin.com/feed/update/urn:li:activity:7488825356494237696/

[e] https://www.dropbox.com/scl/fi/hettphvtpyrksggfect9d/Tutorial-on-Pan-Matrix-Profile.pptx?rlkey=p59gd2w56fxl9kl2fh5q819oo&dl=0

Disclosure: I developed AIStupidLevel, the open-source system used to collect and analyze this data. Both the frontend and backend are MIT-licensed.

Most LLM evaluations measure performance at a single point in time. I wanted to investigate a different question:

How stable are the models behind production APIs over time, and how can sustained performance changes be separated from ordinary stochastic variation?

I built a continuous evaluation pipeline that repeatedly tests models across coding, deep reasoning, tool calling and high-frequency canary tasks.

Dataset and evaluation process

For this analysis, I examined:

• 31,352 hourly benchmark scores
• 49 model identifiers
• Multiple providers and model families
• Repeated measurements using consistent tasks and scoring
• A normalized 0-100 composite score

Coding responses are executed rather than judged only through model-based evaluation. Tool-calling tests require models to select tools, construct valid arguments and complete workflows inside isolated Docker environments.

Tasks are executed five times, with the results aggregated to reduce the influence of unusually strong or weak generations. Prompts, scoring logic and API parameters are kept consistent wherever supported by the provider.

Main result

The observed score variation was:

• Within the same day: 2.8 points
• Between different days: 8.4 points

Between-day variation was therefore approximately 3× greater than within-day variation.

This suggests that isolated hourly movements are dominated by normal model stochasticity, while sustained changes across daily evaluation windows provide a materially stronger signal for detecting performance drift.

The detection pipeline aggregates repeated measurements into daily medians and applies sequential change-point detection. Potential incidents must persist beyond the expected historical variance and pass statistical and minimum-effect thresholds before being classified as degradation or recovery.

Continuous model monitoring

This analysis became the foundation of AIStupidLevel, a continuous LLM benchmarking and drift-detection system.

The complete dataset has now reached:

• 169,858 benchmark runs
• 104,458 measured scores
• 88M+ processed tokens
• 81 historical model identifiers
• 22 models currently monitored
• 6 active providers

The attached screenshot shows the live monitoring interface. Models are classified as stable, volatile, degraded or recovering, with separate measurements for coding, reasoning, tool use, reliability, latency and price.

At the time of the screenshot, the system detected a 32% sustained performance decline in Gemini 3.1 Flash Lite and classified it as a critical incident.

The same continuously updated dataset also powers an OpenAI-compatible router that selects models according to their current task-specific performance, stability, tool-calling reliability, latency and cost.

This adds a missing observability dimension for production LLM systems. Existing monitoring generally captures availability, errors, latency and token cost. Continuous evaluation also measures whether the model remains capable of performing the work for which it was selected.

Project resources:

• Live dataset and dashboard: https://aistupidlevel.info
• Evaluation methodology: https://aistupidlevel.info/methodology
• MIT-licensed frontend: https://github.com/StudioPlatforms/aistupidmeter-web
• MIT-licensed backend/API: https://github.com/StudioPlatforms/aistupidmeter-api

I would be interested in comparing this approach with other temporal evaluation or change-point detection systems being used for production LLM monitoring.

How much of a disadvantage is it if your only internship is not at one of the big frontier labs when it comes to post-phd opportunities in robotics/ML? My PhD is at a top university (UK) and my internship is interesting and relevant but the team itself is smaller and it's no Nvidia/Google/etc. Most places here prefer interns for 6 months so I'm not sure if I can do another internship down the line or if there's even much point compared to just wrapping up the PhD and then getting a job.

Is having a relevant internship already a big plus when it comes to applying to industry, or does it need to be a really well known big tech company?

Hey everyone, I'm an international student studying in the US. I'm on track to graduate late next year. My research is not exactly ML, it is in 3D computer vision but have decent exposure to ML as well.

In case you didn't know, the CPT program (which let's internation students do internships) has been suspended by many top universities (UC Berkeley, UIUC, Purdue, UNC, UCLA, stanford, etc). Given that there is now no way for me to do an internship, how hard will it be for me to get a job when I'm nearing graduation?

I have 3 papers in CVPR, 3DV and ICRA (robotics conference) and hope to publish 2 more at next year's ICCV and neurips before graduating. I'm just worried that all my hardwork will go for a waste because of this policy change (I'm from a 3rd world country, so not much opportunity back home).

To be crystal clear, I'm not asking for legal advice, just wanted to know in your experiance, have you seen anyone (international student) get into good industry labs without internships?

EDIT: thanks so much for everyone for the quick replies! If it helps, my specific research area is 3D reconstruction, and I've been focused on Gaussian Splatting recently, if this info helps anyone help me!