Exploratory Causal Inference in SAEnce

## Abstract

Abstract Randomized Controlled Trials are one of the pillars of science; nevertheless, they rely on hand-crafted hypotheses and expensive analysis.
Such constraints prevent causal effect estimation at scale, potentially anchoring on popular yet incomplete hypotheses.
We propose to discover the unknown effects of a treatment directly from data.
For this, we turn unstructured data from a trial into meaningful representations via pretrained foundation models and interpret them via a sparse autoencoder.
However, discovering significant causal effects at the neural level is not trivial due to multiple-testing issues and effects entanglement.
To address these challenges, we introduce Neural Effect Search , a novel recursive procedure solving both issues by progressive stratification.
After assessing the robustness of our algorithm on semi-synthetic experiments, we showcase, in the context of experimental ecology, the first successful unsupervised causal effect identification on a real-world scientific trial.

### 1 Introduction

In science, data has been historically collected to answer specific questions (Popper, 2005). In this rational view, scientists formulate a hypothesis, often as a causal association, and collect data to falsify it. For example, an experimental ecologist may suspect that exposure to some substance may affect how ants behave, or more in general, “a treatment $T$ has a causal effect on an outcome $Y$”. They then perform a controlled experiment, administering $T$ or a placebo to a number of individuals and check whether there is a significant difference in the correlation between the treatment assignment and the outcome.
While this paradigm has dominated science for centuries, modern science started embracing the creation of atlases: vast, comprehensive maps of natural phenomena, collected for general purposes. Today, we have planetary-scale maps of life genomes (Chikhi et al., 2024), sequencing of 33 different types of cancer (Weinstein et al., 2013), imaging of cells under thousands of perturbations (Sypetkowski et al., 2023) to name a few. Different than the classical paradigm, these datasets call for an empiricist view, starting with exploratory data-driven investigations. The new challenge is that the immense size of these datasets prohibits scientists from just “looking at the data and finding out what is interesting”.
Even beyond atlases, consider the specific example of experimental ecology, where fine-grained social interactions between many individuals are critical to understanding the spread of disease (Finn et al., 2019). Clearly, this can be dramatically accelerated with computer vision, using the predictions of a model as input for causal inference pipelines (Cadei et al., 2025). Still, scientists need to decide what to annotate a priori before they can meaningfully look at and understand the data. This introduces a biasing effect, known as the “Matthew effect” (Merton, 1968) or informally as “rich-get-richer”: scientists are biased by prior successful investigations, e.g., behaviors that they have already studied.

In this paper, we characterize differences and synergies between the classical rationalist view and the emerging empiricist one and propose a method to identify statistically significant effects in exploratory experiments, formally grounding it with the language of statistical causality, see Figure [1](https://arxiv.org/html/2510.14073v1#S0.F1). We formulate this problem as analyzing a randomized controlled trial, where a treatment is administered randomly and the possible effects are measured indirectly, e.g., via imaging or other raw observations. Instead of scientists formulating only a priori hypotheses on the effect, label some data, and train a model to extend labels to the whole dataset (i.e., the rationalist view (Cadei et al., 2024, 2025)), we propose to train sparse autoencoders (SAEs) on the representation of foundation models and generate data-driven effect hypotheses (i.e., empiricist approach) by the interpretation of the significant effects on the neural representations.
In this new paradigm, the main challenge is that, if the SAE is not perfectly disentangled (Elhage et al., 2022), any neuron minimally entangled with the true effect may appear significantly treatment-responsive, which complicates interpretation.
To address it, we propose a novel recursive stratification technique to iteratively correct the effect on entangled neurons.

Looking at the data before committing to any hypothesis, we overcome the Matthew effect, enriching the rationalist view in a data-driven way. We propose to work with pretrained foundation models, training SAEs directly on the target experimental data. This is important because pretrained foundation models can be biased as well, which is problematic for drawing scientific conclusions (Cadei et al., 2024). Instead of directly testing a single hypothesis, our approach enables to preliminary explore thousands of potential effects in a semantically expressive latent space, still allowing the domain experts to interpret, judge and eventually test them a posteriori.
This is in stark contrast with preliminary empiricist approaches in causality like “causal feature learning” (Chalupka et al., 2017), which only commits to a single hypothesis by discrete clustering. Our contributions are:

- •
Within the statistical causality framework, we formally differentiate rationalist and empiricist approaches to causal inference, highlighting their complementary strengths and limitations.
- •
We propose a novel empiricist methodology building on foundation models and sparse autoencoders. We characterize the statistical challenges in multiple hypothesis testing to discover treatment effects over neural representations in our paradox of exploratory causal inference. Then, we introduce a novel iterative hypothesis testing procedure to overcome such challenges.
- •
We showcase in both semi-synthetic (real images but synthetic causal relations) and a real-world trial in experimental ecology that our approach is capable of disentangling and identify the treatment effect in an experiment. To the best of our knowledge, this is the first successful application of sparse autoencoders to causal inference, which we also test in a real-world scientific dataset.

### 2 Treatment Effect Estimation in Randomized Controlled Trials

Notation. In the paper, we refer to random variables as capital letters and their realizations as lowercase letters. Matrices are referred to as upper-case, boldface letters.

Causal Inference.
Causal Inference aims to quantify the effects of an intervention on a certain variable treatment on some outcome variables of interest, see Figure [2](https://arxiv.org/html/2510.14073v1#S2.F2) (left).
For simplicity, we consider a binary treatment $T=\left\{0,1\right\}$ (e.g., taking a placebo or a drug) and outcome variables $Y\in\left\{0,1\right\}^{r}$ (e.g., binary indicators for symptoms, biomarkers, or clinical events). While continuous extensions would be interesting, we focus on discrete outcomes since continuous concepts in SAEs are not well understood yet (Quirke et al., 2025). At population level we aim to estimate the Average Treatment Effect (ATE):

$$ $\tau=\mathbb{E}[Y(T=1)-Y(T=0)],$ (1) $$

where $Y(T=1)$ and $Y(T=0)$, or $Y(1)$ and $Y(1)$ for short, denote the potential outcomes under treatment and control (Rubin, 1974) (equivalently $Y|do(T)=1$ and $Y|do(T)=0$ according to Pearl (2009)).
Estimating $\tau$ is challenging because, for each individual, only one potential outcome is factually observed—the one under the received treatment—so the counterfactual is missing (fundamental problem of causal inference (Holland, 1986)).
This problem is mitigated in the sciences by performing, whenever possible, a Randomized Controlled Trial (RCT). By randomly assigning the treatment, i.e., $T$ has no causes, we prevent spurious correlations between the treatment and any other cause $W\in\mathbb{R}^{q}$ of the outcome (no confounders), allowing to (statistically) identify the ATE with the associational difference, i.e.,

$$ $\tau=\mathbb{E}[Y\mid T=1]-\mathbb{E}[Y\mid T=0],$ (2) $$

under standard causal assumptions (Rubin, 1986) of consistency (observing $T=t$, then $Y=Y(t)$), and no interference across individuals (i.e., all individuals are independent samples from the population, and the treatment assignment to the individual $i$ does not affect individual $j$).
It follows that the difference between the treated and control groups’ sample means is already an unbiased estimator of the ATE. Nonetheless,
more sophisticated estimators such as Augmented Inverse Propensity Weighting (AIPW (Robins et al., 1994)) can achieve lower variance and thus greater efficiency.

Figure: Figure 2: Exemplary graphical models for randomized controlled trials (i.e., no edge from $W$ to $T$). In Causal Inference (left), both $T$ and $Y$ are observed, and $W$ does not influence $T$ as we are assuming a randomized controlled trial. In Prediction-Powered Causal Inference (center), $Y$ is not observed directly but is known and can be partially labeled. The missing $Y$ is predicted by a neural network from high-dimensional $X$ that is trained either on the same trials if labels are available (Cadei et al., 2024) or on other trials with the same label space (Cadei et al., 2025). In Exploratory Causal Inference (right), $Y$ is unknown and unobserved and is discovered by a neural network from high-dimensional $X$ in a purely data-driven way.

Prediction-Powered Causal Inference and the rationalist approach. Assume that $Y$ is not observed directly. Instead, we measure it indirectly via an high-dimensional variable $X\in\mathcal{X}\subseteq\mathbb{R}^{p}$, capturing the affected outcome information, i.e., $H(Y|X)=0$, mixed with the other attributes of the individual $W\in\mathbb{R}^{q}$. For example, in the trial by Cadei et al. (2024), ants are treated with an invisible substance, which affects their grooming behaviors. Ecologists do not record the behaviors directly but rather take videos $X$ of the ant interactions, which they then analyze. Prior work by  Cadei et al. (2024, 2025) showed how to train a model on partially labeled data or similar experiments to predict factual outcomes $\hat{Y}$ from $X$ that approximate $Y$ and then use them for causal inference.
For simplicity, we assume that $T$ is not directly visible in $X$, a common practice in double-blind randomized trials (e.g., neither the patient nor the doctor analyzing the results knows which treatment was assigned).
The set-up is illustrated in Figure [2](https://arxiv.org/html/2510.14073v1#S2.F2) (center). To simplify the notation, we ignore that some covariates $W$ may only influence $X$ and not $Y$. If such covariates exist, we group them into $W$ (having a null causal effect on $Y$).

Exploratory Causal Inference and the empiricist approach. The rationalist view requires knowing what the treatment will affect a priori, which is also prone to the Matthew effect (Merton, 1968) in exploratory experiments (hypotheses are often informed by the outcome of prior successful trials). In this paper, we consider the setting where experiments are exploratory, which we informally model as the scientists having no a priori knowledge of what $Y$ may be. This is shown in Figure [2](https://arxiv.org/html/2510.14073v1#S2.F2) (right), with $Y$ being unobserved and unknown (only measured through $X$). We remark that this problem is related to causal abstraction (Rubenstein et al., 2017; Chalupka et al., 2017). In principle, one may consider the pixels themselves as influenced by the treatment. We instead consider the ground truth $Y$ to be the coarsest possible abstraction of the effect of $T$. In other words, we have that $T\perp\!\!\!\perp W|Y$ and the mutual information $I(Y,X)$ is as small as possible (Achille and Soatto, 2018; Fumero et al., 2023).
With a slight abuse of notation, we do not need to assume that such $Y$ exists, so $r$ can be zero if the treatment has no effect at all. Our goal is to propose candidate effects $Y$ to the scientists in a purely data-driven way, discovering significant statistics that differentiate the treated and control populations. It is important to remark that we do not interpret these statistics as necessarily scientifically relevant. The reason is that, when working with high-dimensional data, there can be irrelevant effects, i.e., visible treatment and (finite sample) experiment design biases. Our approach is to identify all significant statistics and leave the interpretation to the domain experts. The empiricist view should not replace the rationalist one, but enrich it with additional data-driven hypotheses.

### 3 Exploratory Causal Inference via Neural Representations

To detect treatment effects when only high–dimensional indirect outcome measurements $X$ are available, we turn these raw observations into analyzable measurements. We first pass samples $x$ through a pretrained foundation model (FM) (Bommasani et al., 2022), obtaining representations $h=\phi(x)\in\mathbb{R}^{d}$ whose geometry captures semantically meaningful regularities (Amir et al., 2022; Valeriani et al., 2023). Throughout, we assume the FM is *sufficient for the outcome information* (Achille and Soatto, 2018) (i.e.,
$I(X,Y)=I\big(\phi(X),Y\big),$)
so working in $h$ preserves exactly the information about the (unknown) outcome factors $Y$ that is present in the raw data. Under sufficiency, any arm difference that exists in $X$ is detectable in representation space, making $h$ a principled surrogate for measurement.

From FM features to a measurement dictionary.
While FM features are semantically structured, individual coordinates in $h$ generally not align with human–readable concepts (Bricken et al., 2023). We therefore *reparameterize* the representation into a sparse, interpretable measurement dictionary using a sparse autoencoder (SAE) (Bricken et al., 2023; Huben et al., 2024). Intuitively, the SAE expresses each $h$ as a sparse linear combination of atoms that behave like measurable channels; sparsity biases solutions toward localized, approximately monosemantic features that scientists can inspect a posteriori.
Given foundation model’s features $h\in\mathbb{R}^{d}$, the SAE computes a high–dimensional but *sparse* code $z\in\mathbb{R}^{d}$ and reconstructs $h$ linearly:

$$ $z\;=\;f(h)\;=\;g\;\!\big(\mathbf{E}^{\top}h+b_{e}\big),\qquad\hat{{h}}\;=\;\mathbf{D}z+b_{d},$ (3) $$

where $\mathbf{E},\mathbf{D}\in\mathbb{R}^{d\times m}$ are respectively the encoder, and decoder linear maps, $b_{e},b_{d}\in\mathbb{R}^{m}$ are the learnable biases, and $g:\mathbb{R}^{m}\!\to\!\mathbb{R}^{m}$ is the encoder nonlinearity (Bricken et al., 2023). Training minimizes a reconstruction loss with a sparsity penalty $\mathcal{S}$ weighted $\lambda\geq 0$, i.e.,

$$ $\min_{D,z\geq 0}\;\mathbb{E}\big[\|h-\mathbf{D}z-b_{d}\|_{2}^{2}\big]\;+\;\lambda\,\mathcal{S}(z).$ (4) $$

Thereafter, each input can be summarized as ${h}\approx b_{d}+\sum_{j}z_{j}d_{j}$, where $\|z\|_{0}\ll d$ and $\mathbf{D}=[d_{1},\ldots,d_{m}]$. This turns the FM representation into a large dictionary of interpretable channels: each coordinate $z_{j}$ serves as a putative detector of a simple attribute, with still some inevitable leakage (Huben et al., 2024).

Monosemanticity, leakage, and entanglement.
In exploratory experiments, we would like each SAE code coordinate to behave like a single, human–readable measurement channel for a simple outcome factor. When this happens, a scientist can read off “what changed” from the few activated codes. In practice, however, codes often *leak* across factors: one neuron can respond weakly to several distinct attributes, i.e., weak polysemanticity and corresponding *entanglement* (Locatello et al., 2019). We need a minimal language to talk about (i) the direction in code space associated with a factor and (ii) how widely those directions spill across neurons. Let $Z\in\mathbb{R}^{m}$ be SAE codes and $Y=(Y_{1},\dots,Y_{r})$ the (unknown) binary outcome factors with $m\gg r$. To define the leakage set and index, we first define the concept $Y_{k}$ neural representation as:

$$ $v_{k}\;:=\;\mathbb{E}[\,Z\mid do(Y_{k}=1)\,]-\mathbb{E}[\,Z\mid do(Y_{k}=0)\,]\in\mathbb{R}^{m}\quad\forall k\in\{1,...,r\}.$ (5) $$

and we say that the neuron $Z_{j}$ with $j\in\{1,...,m\}$ is *activated* by the factor $Y_{k}$ if $|(v_{k})_{j}|\geq\varepsilon>0$.
When the neural effect representations $\{v_{k}\}_{k=1}^{r}$ are *sparse* and largely *disjoint* across coordinates, each effect factor “lights up” only a few neurons, and different factors rely on different neurons.

###### Definition 3.1 (Leakage set and index) .

Fix a threshold $\varepsilon>0$. In a ECI problem with effect neural representations $\{v_{k}\}_{k=1}^{r}$,
we define the *leakage set* and *leakage index*, respectively, as

$$ $\mathcal{A}_{\varepsilon}\;=\;\bigcup_{k=1}^{r}\{\,j:\,|(v_{k})_{j}|\geq\varepsilon\,\},\qquad\rho_{\varepsilon}\;:=\;\frac{|\mathcal{A}_{\varepsilon}|}{m}.$ (6) $$

If $|\mathcal{A}_{\varepsilon}|\gg r$, i.e., $\rho_{\varepsilon}\gg 0$, it indicates that many neurons respond to multiple factors, i.e., polysemanticity, whereas monosemanticity with respect to $Y$ implies $|\mathcal{A}_{\varepsilon}|=r$, i.e., $\rho_{\varepsilon}\approx 0$.

Codes as statistical measurement channels.
Under FM sufficiency and an (approximately) monosemantic SAE, it becomes natural to pose causal questions at the level of individual codes. If the true affected outcomes $Y$ are perfectly localized in disjoint subsets of coordinates of $Z$, then one can test each coordinate for a treatment–control mean shift using a two–sample $t$–test, applying Bonferroni adjustment (Bonferroni, 1936) to control the family–wise error rate at $\alpha$ regardless of the number of tests $m$. This provides an idealized measurement interface: we can scan $Z$ for treatment–responsive channels and later interpret significant coordinates via the dictionary atoms $d_{j}$.

Challenge: entangled effect representations.
The above picture breaks down when leakage occurs, as any neuron entangled with the true affected outcome will eventually be identified as significantly activated, while $|\mathcal{A}_{\varepsilon}|=O(m)\gg r$, challenging any interpretation.
Intuitively, entangled neurons that are primarily assigned to other concepts still activate differently depending on $Y$, so with more powerful tests (larger sample sizes or stronger causal effects), they would be deemed significantly affected. Thereafter, classical multiplicity correction does not rescue interpretability here, leading to the paradox of Exploratory Causal Inference:

We formalize these two phenomena below. Let $\tau_{j}$ denote the treatment effect on code $j$.

###### Theorem 3.1 (Significance level collapse with sample size) .

Suppose at least $\rho_{\varepsilon}m$ neurons have nonzero effect $|\tau_{j}|\geq\varepsilon>0$. Via multiple testing, regardless of the Bonferroni adjustment,

$$ $\Pr\!\Big[\{\text{all }j\in\mathcal{A}_{\varepsilon}\text{ are rejected}\}\Big]\;\to\;1\quad\text{as }n\to\infty,$ $$

and the number of rejections converges to $\rho_{\varepsilon}m$ in probability.

###### Proof sketch.

For each $j$, the $t$–statistic is asymptotically normal with noncentrality $\lambda_{j}=\sqrt{n}\,\tau_{j}/\sigma$. The Bonferroni cutoff, which determines the significance of $\tau_{j}$, grows like $\sqrt{2\log m}$; this cutoff is dominated by the growth in expectation of $\tau_{j}$ ($\sqrt{n}$ as $n\to\infty$). Hence, any $j$ with $\tau_{j}\neq 0$ is eventually rejected. Without Bonferroni correction, the significance cutoff is constant. See full proof in Appendix [A](https://arxiv.org/html/2510.14073v1#A1).
∎

###### Theorem 3.2 (Significance collapse with effect magnitude) .

Fix $n<\infty$ and let $\tau_{j}(s)=s\,\gamma_{j}$ with $s>0$. Via multiple testing, regardless of the Bonferroni adjustment,

$$ $\Pr\!\Big[\{\text{all }j\in\mathcal{A}_{\varepsilon}\text{ are rejected}\}\Big]\;\to\;1\quad\text{as }s\to\infty,$ $$

and the number of rejections converges to $\rho_{\varepsilon}m$ in probability.

###### Proof sketch.

The noncentrality $\lambda_{j}(s)=\sqrt{n}\,s\gamma_{j}/\sigma$ grows linearly in $s$, while the cutoff, even with Bonferroni correction, is fixed for fixed $m,n$; every $\gamma_{j}\neq 0$ is eventually rejected. Details in Appendix [A](https://arxiv.org/html/2510.14073v1#A1).
∎

Numerical illustration.
Let $T\!\sim\!\mathrm{Bernoulli}(0.5)$, $Y\mid T\!=\!t\sim\mathcal{N}(\tau t,1)$ (single effect), and $Z=[Z_{A},Z_{B}]\in\mathbb{R}^{m}$ where $Z_{A}=Y$ (the effect principal channel) and $Z_{B}\mid Y=y\sim\mathcal{N}\!\big(0.01\,y\,\mathbf{1}_{m-1},\,I_{m-1}\big)$ (entangled channels). As shown in Figure [3](https://arxiv.org/html/2510.14073v1#S3.F3) for 10 seeds, increasing either $n$ or $\tau$ leads all the multiple testing to flag all the weakly entangled $Z_{B}$ coordinates as significant, despite their negligible semantic relevance. This motivates the disentangling, stratified testing procedure introduced next (Section [4](https://arxiv.org/html/2510.14073v1#S4)).

Figure: Figure 3: The Paradox of Exploratory Causal Inference: Increasing the power of the test, the effect on any outcome-entangled code becomes significant, regardless of its main interpretation.
Refer to caption: x2.png

###### Definition 3.1 (Leakage set and index) .

###### Theorem 3.1 (Significance level collapse with sample size) .

###### Proof sketch.

###### Theorem 3.2 (Significance collapse with effect magnitude) .

###### Proof sketch.

### 4 Neural Effect Search

To mitigate the multi-test significance collapse with entangled representation, we propose a novel causally principled algorithm that disentangles the leaked effects by recursive stratification:

Figure: Algorithm 1 Neural Effect Search (NES)

where NeuralEffectTest (Algorithm [2](https://arxiv.org/html/2510.14073v1#alg2)) is the procedure for multi-hypothesis testing on all the neurons $j$, by stratification (with arm-wise residualization) over the already retrieved effects S. See full description in Appendix [B](https://arxiv.org/html/2510.14073v1#A2). The key idea is that if we test all neurons simultaneously, vanilla multiple testing cannot distinguish whether a neuron carries its own causal effect or merely leaks information about another concept. By contrast, NES first recovers the most prominent effect by its most representative neuron, then it *controls* its effect in subsequent tests, preventing the ECI paradox, continuing iteratively.
Since this is a multiple testing setting, in Line 6 we still perform Bonferroni correction by dividing the significance level $\alpha$ by $m$. In practice, if the sample size is very small, one can make the test less conservative by relaxing the correction (which would return more, possibly false positives for the scientist to review).

###### Theorem 4.1 (Consistency of Neural Effect Search) .

Suppose the outcome neural representation, i.e., SAE codes, captures and almost disentangles the $r$ treatment effects (still allowing for broad effect leakage).
Then, as $n\to\infty$, the NES’ output $\texttt{S}_{\text{final}}$ satisfies

$$ $\Pr\!\Big(\texttt{S}_{\text{final}}=\{j_{1},\dots,j_{r}\}\!\Big)\;\longrightarrow\;1,$ $$

where each $j_{k}$ is a neuron coordinate principally aligned with a distinct affected outcome $Y_{k}$.

###### Proof Sketch.

At the first round, entanglement makes several coordinates look affected; nevertheless, the coordinate most aligned with some true direction $v_{k}$ maximizes the treatment effect and, under Bonferroni control, is selected with probability $\to 1$ as $n\to\infty$.
Next, (pooled) stratification removes the contribution of the discovered direction from every coordinate: (i) its leakage into other neurons averages out in expectation, and (ii) the post-treatment conditioning transmitting collider bias get bounded.
Consequently, all remaining adjusted test statistics are mean-zero (up to vanishing error).
By repeating this argument, each iteration peels off one undiscovered principal direction until all $r$ are recovered; thereafter no coordinate exhibits a nonzero mean effect and the procedure halts.
Hence $\Pr\!\big(\texttt{S}_{\text{final}}=\{j_{1},\dots,j_{r}\}\big)\to 1$ and $\mathbb{E}[|\texttt{S}_{\text{final}}|]\to r$. Further efficiency results, without loosing consistency, can be obtained with arm-wise effect residualization by the already selected neurons. See Appendix [A](https://arxiv.org/html/2510.14073v1#A1) for the complete formulation, proof and hypotheses discussion.
∎

Discussion. NES recovers the $r$ effect concepts in probability and terminates, in sharp contrast with the paradox described earlier.
While standard multi-hypothesis tests collapse with increasing power, i.e., $n$ and $\tau$, proposing *all* entangled neurons with $Y$ as significant effects, NES avoids this pitfall by recursively stratifying.
Each iteration removes the spurious signal caused by leakage from already identified effects, bounding the collider bias, so that only the remain effect factor remains detectable.
In this sense, NES does not merely test for effects: it *disentangles* the representation, identifying one true causal factor at a time until the entire effect subspace is recovered.
Thus, NES can be interpreted both as a multiple-testing correction method robust to entanglement and as a principled effect disentanglement algorithm.

###### Theorem 4.1 (Consistency of Neural Effect Search) .

###### Proof Sketch.

### 5 Related Works

Interpretable Heterogeneous Treatment Effect Estimation.
A closely related line of work is the empirical discovery of treatment effect heterogeneity across covariates $W$. Methods such as causal trees, forests, and decision rules ensembles (Athey and Imbens, 2016; Athey et al., 2019; Bargagli-Stoffi et al., 2020) identify subpopulations with different responses, recognizing that pointwise estimation of the Conditional Average Treatment Effect (CATE) is almost impossible to test, and still difficult and risky to interpret. Since $W$ is lower-dimensional, interpretability of these partitions or rules is crucial, and the field has developed around making this empirical exploration scientifically meaningful. Our work is analogous in spirit: instead of asking *who* is affected (heterogeneity over $W$), we ask *what* is affected (discovering affected outcomes $Y$) when the outcome space itself is high-dimensional and initially unknown.

Causal abstractions and representations. In the line of work of causal abstractions, Visual Causal Feature Learning (VCFL, Chalupka et al., 2014) was introduced to discover interventions in data rather than outcomes. In scientific trials, however, treatments are fixed by design, and the challenge is to recover their effects from complex outcome measurements. Causal Feature Learning (CFL, Chalupka et al., 2017) extends this to outcome clustering by grouping micro- to macro-variables using equivalence classes of $P(X\mid do(T))$. This requires density estimation in high-dimensional spaces, which is generally infeasible. While clustering other metrics may be possible, causal feature learning commits to a single grouping rule, while we find all statistically significant ones. Another line of work tackles the discovery of causal variables from high-dimensional observations (Schölkopf et al., 2021). Closest in spirit to our setting are interventional approaches (Varici et al., 2023, 2024; Zhang et al., 2023; Yao et al., 2025), which, even with all the necessary extra assumptions, would only offer identification results for the experimental settings $W$ and not the outcome (i.e., the component invariant to the intervention (Yao et al., 2025)). Therefore, they can not be applied to exploratory causal inference because they cannot discover outcome variables.

Scientific discovery via SAEs.
A related line of work uses SAEs to decompose *polysemantic* hidden representations in foundation models into more *monosemantic* units that align with single concepts (Bricken et al., 2023; Templeton et al., 2024; Huben et al., 2024; Papadimitriou et al., 2025). Although SAEs were initially proposed as an interpretability tool (Bricken et al., 2023), a growing body of negative results, including spurious interpretability on random networks (Heap et al., 2025), failures to isolated atomic concepts (Leask et al., 2025; Chanin et al., 2025), and limited downstream benefits (Wu et al., 2025), casts doubt on whether SAE features faithfully reflect underlying mechanisms rather than post-hoc artifacts. Despite these interpretability concerns, recent work shows that SAEs can still be useful for generating scientific hypotheses from high-dimensional data (Peng et al., 2025). For example, *HypotheSAEs* (Movva et al., 2025) leverage SAEs to surface human-understandable patterns correlated with target outcomes (e.g., engagement levels), which researchers can then treat as hypotheses for follow-up study. Our setting is related but distinct: whereas these approaches focus on correlations and do not provide statistical procedures to test the significance of the unsupervised discoveries, we target *causal* effects and develop inference to assess which high-dimensional outcomes $Y$ are affected, offering principled support for exploratory causal claims.

### 6 Experiments

We validate our analyses (significance collapse paradox, and NES consistency) in two complementary settings: a semi-synthetic benchmark where ground-truth causal effects are known, and a real-world randomized trial from experimental ecology.

#### 6.1 Semi-Synthetic Benchmark

We simulated a family of RCTs $\{T_{i},W_{i},Y_{i}\}_{i=1}^{n}$, relating both the individual covariates and outcomes one-to-one with specific attributes in the CelebA (Liu et al., 2018) dataset, e.g., wearing_hat and eyeglasses, and then assigned a random image $X_{i}$ from the dataset perfectly matching such attributes. Given the corresponding random sample $\{T_{i},X_{i}\}_{i=1}^{n}$ we (i) trained a SAE over the image representations encoded by SigLIP (Zhai et al., 2023), and (ii) tested NES for effect discovery against vanilla statistical tests ($t$-test, FDR (Schweder and Spjøtvoll, 1982), Bonferroni) and top-k effects selection. For quantitative evaluation, we first assessed SAE monosemanticity with respect to the considered CelebA attributes (see Figure [7](https://arxiv.org/html/2510.14073v1#A5.F7)), and extracted the ground truth neurons referring to $Y$. Then, for each effect discovery, we computed Recall, Precision, and Intersection over Union (IoU) with respect to them. Full details about the data generating procedure, training, and evaluation with additional assessment on interpretability and SAE entanglement, together with extensive ablations on method variants, i.e., estimator and test, and hedge cases, i.e., no-effect, are reported in Appendix [D](https://arxiv.org/html/2510.14073v1#A4)-[E](https://arxiv.org/html/2510.14073v1#A5). The main results ($r=2$) are summarized in Figure [4](https://arxiv.org/html/2510.14073v1#S6.F4).

Figure: Figure 4: Semi-synthetic benchmark. Precision, Recall, and IoU of different testing procedures across sample size $N$ (top) and effect size $\tau$ (bottom). NES consistently achieves the best trade-off, avoiding the significance collapse of standard corrections.
Refer to caption: x3.png

Results.
Increasing the power of the tests (increasing the sample size $n$ or effect magnitude $\tau$), all the methods eventually retrieve the true significant effects, i.e., Recall $\rightarrow 1$. However, while all the baselines drop the Precision and corresponding IoU (Paradox of Exploratory Causal Inference), NES is the only method that mitigates such entanglement biases. As expected, the Paradox doesn’t emerge with very small sample ($n=30$) and effect regime ($\tau=0.1$), and more explorative approaches, as vanilla $t$-test or top-$k$ selection, could be preferred, at the price of potentially more false significant hypotheses, i.e., Precision $\ll 1$. With a yellow dot, we report the performance of each method assuming the number of affected outcomes $r$ is known.
NES still manages to find both effects most of the time. Instead, all the baseline methods fail to reach Precision and Recall above $0.5$: they succeed in retrieving the most significant effect (equivalent to the first step in NES), but then get confounded by the entanglement and miss the second one. While this is clearly a toy experiment, this is undesirable. For example, if in real trials there are multiple effects with different magnitudes (e.g., the positive effect of a drug on the health metric of interest and rare side effects) the leakage of strong effects may prevail over the weaker ones, which would then be missed.

#### 6.2 Real-World Randomized Trial from Experimental Ecology

ISTAnt (Cadei et al., 2024) is an ecological experiment where ants from the same colony are randomly exposed to a treatment or a control substance and continuously filmed in triplets in a closed environment to study the concept of Social Immunity. The biologists are interested in identifying which latent behaviors are significantly affected by treatment. According to previous analysis, we first encoded each frame in the trial with DINOv2 (Oquab et al., 2023), and then we trained a SAE directly on the trial data. NES is then applied without Bonferroni adjustment due to the small sample size ($n=44$ videos) to discover treatment-sensitive codes, and only two neurons are returned.

Figure: Figure 5: Exploratory Causal Inference for Experimental Ecology. Without any knowledge of the behaviors of interest, our procedure retrieves two significant treatment effects, i.e., grooming and background, in agreement with previous literature.
Refer to caption: x4.png

Results. Figure [5](https://arxiv.org/html/2510.14073v1#S6.F5) qualitatively summarizes the interpretations of such neurons, visualizing their corresponding most and least activated clips in the dataset. In agreement with the previous analysis on the dataset (Cadei et al., 2024, 2025), the first neuron retrieved (code 394) represents the grooming event, already measured as significantly affected by the treatment in any previous rationalist approach to the experiment, i.e., actually manually annotating and testing for it.
Quantitatively, such a neuron is exactly the most predictive neuron for grooming event (F1-score=0.398) out of all the 4608 SAE’s codes, confirming the consistent results of our pipeline. We remark that our focus is on the identification of the effect as statistically significant. The imperfect F1-$score$ means that one should not compute treatment effects directly on the neural activation, e.g., without further labeling.
The second neuron activated (code 550) represents the palette background (top right black color mark in the top left position in the first 4 batches of videos), which strongly correlates with the treatment due to the small experiment size (as discussed in the annotation bias by Cadei et al. (2024)).
The fact that the model also identifies the effect of the treatment on the background due to the small sample size is a strength of the method: it is a statistically significant signal, and we want to retrieve it in addition to the behaviors since it is present in the dataset. Domain experts can select which signal is scientifically relevant and even use this information to improve their experimental settings.

### 7 Conclusion

In this paper, we have discussed how foundation models and SAEs can address the challenges of exploratory causal inference, serving as learned measurement devices. A key challenge is that SAE neurons may not map one-to-one onto high-level concepts, and even weak or mixed associations propagate the dependency on the treatment. This means that many neurons can be activated, making the interpretation difficult as they do not encode a single concept, and they activate more with larger sample sizes or stronger effects. We address this issue with Neural Effect Search, a statistical hypothesis testing procedure that iteratively controls for the biased dependency between neurons after they have been selected.
Our experiments on semi-synthetic and real-world randomized trials are encouraging: our method uncovers both scientifically relevant effects and, when present, interpretable associations like background effects due to finite samples that experts can readily dismiss. Overall, we view this work as a first step toward AI-driven efficiency gains in exploratory data science, where foundation models can “look at massive amounts of data first” and then domain experts can identify which patterns have scientific value.

Our approach has several limitations. First, we strongly assume that the observed variables $X$ adequately capture information about the unknown $Y$, i.e., data sufficiency.
For example, shrinkage in a tumor is detectable via X-ray imaging, but, depending on the tumor type, a treatment may also reduce its metabolic activity, which is measured with PET scans. More complex measurement processes for $X$, e.g., multi-modal are a natural extension of our work.
Furthermore, we assume foundation models encode concepts linearly and that SAEs can approximately recover the effects. We believe the linear representation hypothesis (Park et al., 2023) is mild: even if current foundation models are imperfect, future iterations are likely to improve. The good “identifiability” assumption is our strongest. Promising early work already exists (Cui et al., 2025; Hindupur et al., 2025), but the identifiability theory of SAEs is not currently as well understood as that of causal representations (Yao et al., 2025), e.g., still unclear how to deal with continuous concepts. In our paper, we took a more empirical and future-looking stance on improvements in SAEs, focusing on inevitable finite samples entanglement while leveraging pretrained foundation models. Lacking identifiability means that domain experts can today only use our method “as a rescue system for hypotheses they may have missed”, before properly annotating the data and following the rationalist approach. We hope that our work will serve as a practical motivation for future work on identifiability in foundation model representations and SAE.

### Acknowledgments

We thank the Causal Learning and Artificial Intelligence group at ISTA for the continuous feedback on the project and valuable discussions. We further acknowledge the Fourth Bellairs Workshop on Causal Representation Learning held at the Bellairs Research Institute, February 14$/$21, 2025, and particularly the discussions with Chandler Squires, Dhanya Sridhar, Jason Hartford, and
Frederick Eberhardt.
Riccardo Cadei is supported by a Google Research Scholar Award and a Google Google-initiated gift to Francesco Locatello.
Tommaso Mencattini was supported by the ISTernship program.
This research was funded in part by the Austrian Science Fund (FWF) 10.55776/COE12). It was further partially supported by the ISTA Interdisciplinary Project Committee for the collaborative project “ALED” between Francesco Locatello and Sylvia Cremer.
For open access purposes, the author has applied a CC BY public copyright license to any author-accepted manuscript version arising from this submission.

### Ethics Statement

All datasets used in this work are publicly available. In particular, the ISTAnt dataset (Cadei et al., 2024) was annotated and pre-processed by domain experts. While our model is capable of detecting statistically significant signals in randomized trials, the conclusions should not be interpreted as scientifically relevant unless domain experts interpret them. Since we cannot guarantee identifiability, it should only be used as a rescue system for hypotheses that may have been missed before committing to the rationalist approach, which is still necessary.

### Reproducibility Statement

Together with the paper, we submitted the code for NES, which can be used on top of any library for SAEs. A snipped Python implementation for the main algorithm is also presented in Appendix [C](https://arxiv.org/html/2510.14073v1#A3). Standalone code to reproduce all experiments will be released with the final version of the paper. All the datasets we use are publicly available and experiment details are thoroughly detailed in Appendix [D](https://arxiv.org/html/2510.14073v1#A4).

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## Appendix

### Appendix A Proofs

#### A.1 Significance level collapse with sample size (Theorem 3.1 )

###### Theorem A.1 (Significance level collapse with sample size) .

Let $Z\in\mathbb{R}^{m}$ be SAE codes and $\tau_{j}$ the treatment effect on neuron $j$.
By definition

$$ $\mathcal{A}_{\varepsilon}:=\{\,j:|\tau_{j}|\geq\varepsilon\,\},\qquad|\mathcal{A}_{\varepsilon}|=\rho_{\varepsilon}m.$ (7) $$

In multiple testing at level $\alpha$, regardless of Bonferroni correction

$$ $\Pr\!\Big(\text{all }j\in\mathcal{A}_{\varepsilon}\text{ are rejected}\Big)\;\to\;1\quad\text{as }n\to\infty,$ (8) $$

and the number of rejections $R_{n}$ satisfies

$$ $R_{n}\;\to\;\rho_{\varepsilon}m\quad\text{in probability}.$ (9) $$

In words: as the sample size grows, all entangled neurons with the (true) affected outcomes are declared significantly affected by the treatment, regardless of being principally related to other concepts.

###### Proof.

For each neuron $j$, let $\hat{\tau}_{j}$ be the estimated treatment effect and $t_{j}$ its $t$-statistic.
Under standard randomization, we have the asymptotic distribution

$$ $t_{j}\;\;\stackrel{{\scriptstyle d}}{{\to}}\;\;\mathcal{N}(\lambda_{j},1),\qquad\lambda_{j}=\tfrac{\sqrt{n}}{\sigma}\,\tau_{j},$ (10) $$

where $\sigma^{2}$ is the asymptotic variance of $\hat{\tau}_{j}$.

Multiple testing with Bonferroni adjustment rejects $H_{0j}:\tau_{j}=0$ if $|t_{j}|>z_{\alpha/(2m)}$, where $z_{\alpha/(2m)}$ is the $(1-\alpha/(2m))$ quantile of $\mathcal{N}(0,1)$.
As $m\to\infty$, the threshold satisfies

$$ $z_{\alpha/(2m)}\;\asymp\;\sqrt{2\log m}.$ (11) $$

For any $j\in\mathcal{A}_{\varepsilon}$, we have $\tau_{j}\neq 0$, hence $\lambda_{j}$ diverges at rate $\sqrt{n}$ as $n\to\infty$.
Since $\sqrt{n}$ grows faster than $\sqrt{\log m}$, it follows that

$$ $\Pr\!\big(|t_{j}|>z_{\alpha/(2m)}\big)\;\to\;1.$ (12) $$

Therefore, for all $j\in\mathcal{A}_{\varepsilon}$, the null is rejected with probability tending to one, and analogously

$$ $\Pr\!\big(|t_{j}|>z_{\alpha/2}\big)\;\to\;1.$ (13) $$

without Bonferroni adjustment.
By the union bound,

$$ $\Pr\!\Big(\text{all }j\in\mathcal{A}_{\varepsilon}\text{ are rejected}\Big)\;\to\;1.$ (14) $$

Hence, the number of rejections converges in probability to $|\mathcal{A}_{\varepsilon}|=\rho_{\varepsilon}m$, proving the claim.
∎

###### Theorem A.1 (Significance level collapse with sample size) .

###### Proof.

#### A.2 Significance collapse with effect magnitude (Corollary 3.2 )

###### Corollary A.1 (Significance collapse with effect magnitude) .

Fix a finite sample size $n$.
Suppose the treatment effects scale as

$$ $\tau_{j}(s)=s\,\gamma_{j},\qquad j=1,\dots,m,$ (15) $$

where $s>0$ is a scaling parameter and $\gamma_{j}$ are fixed coefficients.
By definition

$$ $\mathcal{A}_{\varepsilon}:=\{\,j:|\gamma_{j}|>\frac{\varepsilon}{s}\,\},\qquad|\mathcal{A}_{\varepsilon}|=\rho_{\varepsilon}m.$ (16) $$

In multiple testing at level $\alpha$ regardless of the Bonferroni correction,

$$ $\Pr\!\Big(\text{all }j\in\mathcal{A}_{\varepsilon}\text{ are rejected}\Big)\;\to\;1\quad\text{as }s\to\infty,$ (17) $$

and the number of rejections $R_{s}$ satisfies

$$ $R_{s}\;\to\;\rho_{\varepsilon}m.\quad\text{in probability}.$ (18) $$

In words: even at a fixed sample size, amplifying the effect magnitude all the entangled neurons with the (true) affected outcomes are declared significantly affected by the treatment, regardless of being principally related to other concepts.

###### Proof.

For neuron $j$, the noncentrality parameter of the $t$-statistic under effect scaling $s$ is

$$ $\lambda_{j}(s)=\tfrac{\sqrt{n}}{\sigma}\,\tau_{j}(s)=\tfrac{\sqrt{n}}{\sigma}\,s\gamma_{j}.$ (19) $$

If $\gamma_{j}=0$, then $\lambda_{j}(s)=0$ for all $s$ and the rejection probability remains bounded by $\alpha/m$.

If $\gamma_{j}\neq 0$, then $\lambda_{j}(s)\to\infty$ linearly in $s$, while the Bonferroni threshold $z_{\alpha/(2m)}$ is fixed (since $n,m$ are fixed).
Therefore,

$$ $\Pr\!\big(|t_{j}|>z_{\alpha/(2m)}\big)\;\to\;1\quad\text{as }s\to\infty.$ (20) $$

Analogously, without Bonferroni $\frac{1}{m}$ significance correction.
Thus, for every $j\in\mathcal{A}_{\varepsilon}$, the null is eventually rejected with probability tending to one.
By independence of limits,

$$ $\Pr\!\Big(\text{all }j\in\mathcal{A}_{\varepsilon}\text{ are rejected}\Big)\;\to\;1,$ (21) $$

and $R_{s}\to\rho_{\varepsilon}m$ in probability, completing the proof.
∎

###### Corollary A.1 (Significance collapse with effect magnitude) .

###### Proof.

#### A.3 Consistency of Neural Effect Search (Theorem 4.1 )

Given a Randomized Controlled Trial, with randomized treatment
$T\in\{0,1\}$, (unobserved) affected outcome $Y\in\mathbb{R}^{r}$, i.e., with non-null effect, and the SAE codes $Z\in\mathbb{R}^{m}$ characterizing each individual/observation extracted from the indirect outcome measurements $X\in\mathcal{X}\subseteq\mathbb{R}^{p}$(^1^11As a special case, the following arguments also hold for binary affected outcomes and neuronal representations in SAE.)
By design (RCT), we furtherly assume SUTVA and finite second moments with standard Lindeberg regularity within strata.
Let the average treatment effect on the (ground truth) outcome be:

$$ $\tau^{Y}:=\mathbb{E}\!\left[Y\mid do(T{=}1)\right]-\mathbb{E}\!\left[Y\mid do(T{=}0)\right]\in\mathbb{R}^{r},$ (22) $$

and the average treatment effect on the SAE codes:

$$ $\tau^{Z}:=\mathbb{E}\!\left[Z\mid do(T{=}1)\right]-\mathbb{E}\!\left[Z\mid do(T{=}0)\right]\in\mathbb{R}^{m},$ (23) $$

then,

$$ $\tau^{Z}\;=\;\sum_{k=1}^{r}\tau^{Y}_{k}\,v_{k}\;=\;V\,\tau^{Y},$ (24) $$

where the matrix $V=[v_{1}~\cdots~v_{r}]\in\mathbb{R}^{m\times r}$ aggregates in columns the $r$ affected outcome neural representations (see Definition in Section [3](https://arxiv.org/html/2510.14073v1#S3)).

###### Assumption A.1 (Sufficiency) .

The matrix of code-level effect directions $V$ has full column rank, i.e., $\mathrm{rank}(V)=r$.

Discussion.
By the neural treatment effect decomposition, i.e., Equation [24](https://arxiv.org/html/2510.14073v1#A1.E24), every code-level contrast lies in $\mathrm{span}\{v_{1},\dots,v_{r}\}$. Assumption [A.1](https://arxiv.org/html/2510.14073v1#A1.Thmassumption1) guarantees this span is truly $r$-dimensional (nondegenerate) and that the linear map $\tau^{Y}\mapsto\tau^{Z}$ is injective—distinct effect vectors $\tau^{Y}$ produce distinct code-level contrasts. Informally, at the *mean-effect* level this behaves like “no loss of information” about $\tau^{Y}$ when passing through $V$ (akin to a sufficient statistic for $\tau^{Y}$ in a parametric family).

###### Assumption A.2 (Alignment) .

There exist *distinct* indices $j_{1},\dots,j_{r}\in[m]$ such that

$$ $|v_{k,j_{k}}|\;>\;\max_{\ell\neq k}|v_{\ell,j_{k}}|\qquad\forall k\in[r],$ (25) $$

each effect direction $v_{k}$ has a distinct principal neuron $j_{k}$ that strictly dominates the other effect directions by *max*. In addition, the following *global Principal–Max* property holds for the realized effect vector $\tau^{Y}$:

$$ $\max_{j\in[m]}\Big|\sum_{\ell=1}^{r}\tau^{Y}_{\ell}\,v_{\ell j}\Big|\;=\;\max_{k\in[r]}\Big|\sum_{\ell=1}^{r}\tau^{Y}_{\ell}\,v_{\ell,\,j_{k}}\Big|.$ (26) $$

Discussion.
Equation [25](https://arxiv.org/html/2510.14073v1#A1.E25) supplies a distinct principal neuron (geometric dominance by max) per affected outcome factor. The global Principal–Max condition [26](https://arxiv.org/html/2510.14073v1#A1.E26) states that, in population, the overall argmax of the code-level contrast $\tau^{Z}=V\tau^{Y}$ is attained at *some* principal neuron. Because each NES round removes discovered effects from the sum, replacing $\sum_{\ell=1}^{r}$ in Equation [26](https://arxiv.org/html/2510.14073v1#A1.E26) by a subsum over the remaining (undiscovered) indices only reduces nonprincipal candidates; hence the argmax remains principal at every round.

###### Assumption A.3 (Arm-wise Effect Decomposition with $\varepsilon$ -Leakage) .

For any NES round $\ell$ with discovered set $\texttt{S}_{\ell-1}{:=}\texttt{S}$ and any $j\notin\texttt{S}$,

$$ $\mathbb{E}\!\left[Z_{j}\,\middle|\,Z_{\texttt{S}},\,do(T{=}t)\right]\;=\;h_{j,t}(Z_{\texttt{S}})\;+\;\rho_{j,t},\qquad t\in\{0,1\},$ (27) $$

where $h_{j,t}$ is measurable w.r.t. $\sigma(Z_{\texttt{S}})$ ($\sigma$-algebra), and

$$ $\rho_{j,1}-\rho_{j,0}\;=\;\sum_{k\notin K(\texttt{S})}\tau^{Y}_{k}\,v_{k,j},$ (28) $$

with $K(\texttt{S})$ the affected outcome components already identified by S.
Moreover, let $G:=g(Z_{\texttt{S}})$ be the pooled (treatment-agnostic) stratification. Define the arm/stratum discrepancy

$$ $\Delta_{j,t}(g):=\mathbb{E}[Z_{j}\mid G{=}g,\,T{=}t]-\mathbb{E}[Z_{j}\mid G{=}g,\,do(T{=}t)].$ $$

with vanishing transport error, after all affected outcome components are identified (i.e., when $K(\texttt{S})=\{1,\dots,r\}$):

$$ $\Delta_{j,t}(g)=0\quad\text{for all }j\notin\texttt{S},\ g\in\mathcal{G},\ t\in\{0,1\}$ (29) $$

There exists a constant $\varepsilon\geq 0$ such that, for the weights $w_{g}$ used by the estimator,

$$ $\Bigg|\sum_{g}w_{g}\Big(\Delta_{j,1}(g)-\Delta_{j,0}(g)\Big)\Bigg|\ \leq\ \varepsilon\qquad\text{for all }j\notin\texttt{S}.$ (30) $$

Finally, to ensure that principal coordinates remain identifiable in the presence of leakage, assume the (population) principal margin

$$ $\Gamma\;:=\;\max_{k\in[r]}\Big|\tau^{Y}_{k}\,v_{k,j_{k}}\Big|\;-\;\max_{j\notin\{j_{1},\dots,j_{r}\}}\Big|\sum_{\ell=1}^{r}\tau^{Y}_{\ell}\,v_{\ell j}\Big|$ (31) $$

satisfies $\Gamma>2\varepsilon$.

Discussion.
Assumption [A.3](https://arxiv.org/html/2510.14073v1#A1.Thmassumption3) is a *mean-level* conditional requirement: conditioning within arms on the already-selected codes $Z_{\texttt{S}}$ explains their contribution in expectation, leaving only undiscovered effects in the adjusted contrast. In addition, Equation [30](https://arxiv.org/html/2510.14073v1#A1.E30) is a mild *pooled-strata transport* bound: even though $G$ is post-treatment and may induce a collider opening, the *weighted* difference between observed and interventional arm means within strata is uniformly bounded by $\varepsilon$ and vanishing. In the linear (or locally linear) regime, the Jacobian of the mapping $Y\mapsto Z$ satisfies $\partial Z/\partial Y=V$ (or more generally $\partial\,\mathbb{E}[Z\mid Y,do(T)]/\partial Y=V$), so the columns $v_{k}$ are Jacobian columns; Assumption [A.2](https://arxiv.org/html/2510.14073v1#A1.Thmassumption2) requires principal dominance, while Assumption [A.3](https://arxiv.org/html/2510.14073v1#A1.Thmassumption3) ensures additive mean structure and bounded transport error so that stratification cancels already-discovered parts up to a uniform $\varepsilon$ bias.

###### Theorem .

Under randomization, SUTVA, finite second moments with Lindeberg regularity, and Assumptions [A.1](https://arxiv.org/html/2510.14073v1#A1.Thmassumption1)–[A.3](https://arxiv.org/html/2510.14073v1#A1.Thmassumption3),
NES with pooled stratification on $Z_{\texttt{S}}$ and Bonferroni control selects one new direction per round and halts after $r$ rounds with probability $\to 1$, identifying all the principal components, i.e.,

$$ $\Pr\!\big(\texttt{S}_{\mathrm{final}}=\{j_{1},\dots,j_{r}\}\big)\to 1,\qquad\mathbb{E}[|\texttt{S}_{\mathrm{final}}|]\to r.$ $$

We proceed by proving NES consistency, decomposing it in the following four steps:

- 1.
average neural treatment effect identification by randomization and SUTVA, i.e., RCT,
- 2.
neural effect estimation by *pooled* stratification is unbiased up to a uniform $\varepsilon$ and, by Assumption [A.3](https://arxiv.org/html/2510.14073v1#A1.Thmassumption3), cancels the contribution of already-discovered directions up to $\varepsilon$, leaving only the undiscovered part,
- 3.
at each round the largest adjusted coordinate identifies, i.e., principal neuron, a new affected outcome by Assumption [A.2](https://arxiv.org/html/2510.14073v1#A1.Thmassumption2) and is detected under standard CLT scaling,
- 4.
by Assumption [A.1](https://arxiv.org/html/2510.14073v1#A1.Thmassumption1), after $r$ rounds no adjusted mean contrast remains beyond $\varepsilon$ and NES halts.

Step 1: Average neural treatment effect identification by randomization.

###### Proposition A.1 (Average Neural Treatment Effect Identification) .

For each coordinate $j$,

$$ $\tau^{Z}_{j}=\mathbb{E}[Z_{j}\mid do(T{=}1)]-\mathbb{E}[Z_{j}\mid do(T{=}0)]=\mathbb{E}[Z_{j}\mid T{=}1]-\mathbb{E}[Z_{j}\mid T{=}0].$ (32) $$

###### Proof.

Randomization implies $P(Z\mid do(T{=}t))=P(Z\mid T{=}t)$. Taking expectations and using SUTVA yields Equation [32](https://arxiv.org/html/2510.14073v1#A1.E32).
∎

Step 2: Neural Effect estimation by pooled stratification: bounded bias and disentanglement.

At round $\ell=1$, $\texttt{S}=\varnothing$, there is no stratification, and the corresponding associational difference identifies the average treatment effect by standard RCT results (shown in Proposition [A.1](https://arxiv.org/html/2510.14073v1#A1.Thmproposition1)).
At round $\ell>1$, build strata $\mathcal{G}$ by deterministically binning $Z_{\texttt{S}}$ (pooled quantile cutpoints, ignoring $T$). For each stratum $g\in\mathcal{G}$ and arm $t\in\{0,1\}$, let $\overline{Z}_{j,tg}$ denote the sample mean of $Z_{j}$ among units with $(T=t,\ G=g)$, and $n_{tg}$ their count.

For each $j\notin\texttt{S}$, define the post-stratified estimator

$$ $\widehat{\tau}^{\mathrm{strat}}_{j}\;=\;\sum_{g\in\mathcal{G}}w_{g}\big(\overline{Z}_{j,1g}-\overline{Z}_{j,0g}\big),\qquad w_{g}\propto n_{1g}+n_{0g},$ (33) $$

see Algorithm [2](https://arxiv.org/html/2510.14073v1#alg2) for weight definition. Across $j\notin\texttt{S}$, use Bonferroni level $\alpha/m$ and add the top-$|\widehat{\tau}^{\mathrm{strat}}_{j}|$ rejection.

###### Lemma A.1 (Neural Effect estimation by pooled stratification: bounded bias and disentanglement) .

Let $\widehat{\tau}^{\mathrm{strat}}_{j}$ be defined by Equation [33](https://arxiv.org/html/2510.14073v1#A1.E33).
Then

$$ $\mathbb{E}\!\left[\widehat{\tau}^{\mathrm{strat}}_{j}\right]=\sum_{g\in\mathcal{G}}\Pr(G{=}g)\!\left(\mathbb{E}[Z_{j}\mid G{=}g,do(T{=}1)]-\mathbb{E}[Z_{j}\mid G{=}g,do(T{=}0)]\right)\;+\;B_{j},$ (34) $$

where the leakage bias

$$ $B_{j}\;:=\;\sum_{g\in\mathcal{G}}w_{g}\Big(\Delta_{j,1}(g)-\Delta_{j,0}(g)\Big)$ $$

satisfies $|B_{j}|\leq\varepsilon$ by Equation [30](https://arxiv.org/html/2510.14073v1#A1.E30). Under Assumption [A.3](https://arxiv.org/html/2510.14073v1#A1.Thmassumption3), the contribution explained by $Z_{\texttt{S}}$ averages out within arm in the interventional means, giving

$$ $\Bigg|\ \mathbb{E}\!\left[\widehat{\tau}^{\mathrm{strat}}_{j}\right]\;-\;\sum_{k\notin K(\texttt{S})}\tau^{Y}_{k}\,v_{k,j}\ \Bigg|\ \leq\ \varepsilon.$ (35) $$

Moreover, under finite second moments and Lindeberg regularity, the $t$-statistic of $\widehat{\tau}^{\mathrm{strat}}_{j}$ is asymptotically normal with variance consistently estimated by the usual post-stratified Neyman formula.

###### Proof.

Add and subtract $\mathbb{E}[Z_{j}\mid G{=}g,do(T{=}t)]$ inside each arm/stratum mean to obtain Equation [34](https://arxiv.org/html/2510.14073v1#A1.E34) and identify $B_{j}$. Assumption [A.3](https://arxiv.org/html/2510.14073v1#A1.Thmassumption3) yields Equation [27](https://arxiv.org/html/2510.14073v1#A1.E27) and Equation [28](https://arxiv.org/html/2510.14073v1#A1.E28), so averaging over $G$ cancels the $h_{j,t}(Z_{\texttt{S}})$ part and preserves the stratum-invariant $\rho_{j,t}$, whose contrast equals Equation [28](https://arxiv.org/html/2510.14073v1#A1.E28); combining with $|B_{j}|\leq\varepsilon$ gives Equation [35](https://arxiv.org/html/2510.14073v1#A1.E35). The CLT follows from standard post-stratified difference-in-means theory with finite second moments and nonvanishing stratum proportions.
∎

Step 3: NES one-step correctness.

###### Proposition A.2 (One-step correctness) .

Suppose the discovered set S retrieves exactly the principal neurons for the $K(\texttt{S})$ affected outcome factors already identified.
Then for any $j\notin\texttt{S}$,

$$ $\Big|\ \mathbb{E}[\widehat{\tau}^{\mathrm{strat}}_{j}]-\sum_{k\notin K(\texttt{S})}\tau^{Y}_{k}\,v_{k,j}\ \Big|\leq\varepsilon.$ $$

By Assumption [A.2](https://arxiv.org/html/2510.14073v1#A1.Thmassumption2) and the margin condition $\Gamma>2\varepsilon$ in Assumption [A.3](https://arxiv.org/html/2510.14073v1#A1.Thmassumption3), the largest adjusted coordinate identifies, i.e., principal neuron, a new affected outcome and is rejected, i.e., selected as significantly affected by the treatment, with probability $\to 1$ as $n\to\infty$.

###### Proof.

By Lemma [A.1](https://arxiv.org/html/2510.14073v1#A1.Thmlemma1), the adjusted mean at $j$ equals the sum over undiscovered directions up to $\pm\varepsilon$. Fix an undiscovered $k^{\star}$ and its principal coordinate $j_{k^{\star}}$ given by Assumption [A.2](https://arxiv.org/html/2510.14073v1#A1.Thmassumption2). The principal margin $\Gamma>2\varepsilon$ ensures that the principal signal at $j_{k^{\star}}$ dominates the maximal nonprincipal signal by more than $2\varepsilon$, hence remains strictly largest after a $\pm\varepsilon$ perturbation. Its $t$-statistic diverges at rate $\sqrt{n}$, so the maximizer over $j\notin\texttt{S}$ is a true undiscovered coordinate with probability $\to 1$.
∎

Step 4: NES consistency by induction.

###### Theorem (NES Consistency) .

Under randomization, SUTVA, finite second moments with Lindeberg regularity, and Assumptions [A.1](https://arxiv.org/html/2510.14073v1#A1.Thmassumption1)–[A.3](https://arxiv.org/html/2510.14073v1#A1.Thmassumption3),
NES with pooled stratification on $Z_{\texttt{S}}$ and Bonferroni control selects one new direction per round and halts after $r$ rounds with probability $\to 1$, identifying all the principal neurons, i.e.,

$$ $\Pr\!\big(\texttt{S}_{\mathrm{final}}=\{j_{1},\dots,j_{r}\}\big)\to 1,\qquad\mathbb{E}[|\texttt{S}_{\mathrm{final}}|]\to r.$ $$

###### Proof.

We distinguish between no affected outcomes, i.e., $r=0$ and at least one, i.e., $r\geq 1$.

- •
If $r=0$ (trivial), then $\tau^{Y}=0$ and by Equation [24](https://arxiv.org/html/2510.14073v1#A1.E24) also $\tau^{Z}=0$. Hence all adjusted expectations are 0, no coordinate is selected at any round, and $\texttt{S}_{\mathrm{final}}=\varnothing$ with probability $\to 1$ as $n\to\infty$.
- •
If $r\geq 1$ with $\tau^{Y}_{k}\neq 0$ for each $k\in\{1,\dots,r\}$:
*Base step.*
This is the special case of Proposition [A.2](https://arxiv.org/html/2510.14073v1#A1.Thmproposition2) with $\texttt{S}=\varnothing$: the largest neural effect identifies a principal direction and is rejected with probability $\to 1$ as $n\to\infty$.
*Induction step.*
Suppose at the beginning of round $\ell$ ($1<\ell\leq r$) the discovered set S identifies exactly the $\ell-1$ distinct principal neurons identifying $K(\texttt{S})$.
By Lemma [A.1](https://arxiv.org/html/2510.14073v1#A1.Thmlemma1),
$\Big|\ \mathbb{E}\big[\widehat{\tau}^{\mathrm{strat}}_{j}\big]\;-\;\sum_{k\notin K(\texttt{S})}\tau^{Y}_{k}\,v_{k,j}\ \Big|\ \leq\ \varepsilon\qquad\text{for every }j\notin\texttt{S},$
i.e., the adjusted mean at any candidate coordinate depends only on undiscovered directions up to a uniform $\varepsilon$ bias. Pick any undiscovered $k^{\star}\notin K(\texttt{S})$ and its principal coordinate $j_{k^{\star}}$ (Assumption [A.2](https://arxiv.org/html/2510.14073v1#A1.Thmassumption2) still applies to the remaining columns). By the margin condition $\Gamma>2\varepsilon$, the associated $t$-statistic diverges and the maximizer over $j\notin\texttt{S}$ is tied to an undiscovered direction with probability $\to 1$.
*Termination.*
Each round adds one previously undiscovered direction with probability $\to 1$.
By Assumption [A.1](https://arxiv.org/html/2510.14073v1#A1.Thmassumption1) ($\mathrm{rank}(V)=r$), there are exactly $r$ linearly independent effect directions; after $r$ rounds they are all represented, and Lemma [A.1](https://arxiv.org/html/2510.14073v1#A1.Thmlemma1) together with the final-stage exactness equation [29](https://arxiv.org/html/2510.14073v1#A1.E29) yields
$\mathbb{E}\big[\widehat{\tau}^{\mathrm{strat}}_{j}\big]=0\qquad\text{for every remaining }j.$
Hence the corresponding $t$-statistics are $O_{p}(1)$ and, under Bonferroni control, no hypothesis is rejected with probability $\to 1$.
Thus no further selections occur, and
$\Pr\big(\texttt{S}_{\mathrm{final}}=\{j_{1},\dots,j_{r}\}\big)\to 1$
and
$\mathbb{E}[|\texttt{S}_{\mathrm{final}}|]\to r.$
Comment.
If a pre-treatment effect modifier $W$ influences the codes used to stratify (i.e., $W\!\to\!Z_{\mathcal{S}}$), pooled conditioning can create transport discrepancies; in that case, if some additional SAE code outside $\mathcal{S}$ captures (part of) this modifier, the same margin argument ensures it will be selected, enlarge $\mathcal{S}$, and—by Equation [29](https://arxiv.org/html/2510.14073v1#A1.E29)—the discrepancy collapses thereafter.
Conversely, if no such modifier projects into the stratification variables (i.e., $W\not\to Z_{\mathcal{S}}$), then $\Delta_{j,t}(g)\equiv 0$ already and no leakage arises.

∎

###### Assumption A.1 (Sufficiency) .

###### Assumption A.2 (Alignment) .

###### Assumption A.3 (Arm-wise Effect Decomposition with ε \varepsilon -Leakage) .

###### Theorem .

###### Proposition A.1 (Average Neural Treatment Effect Identification) .

###### Proof.

###### Lemma A.1 (Neural Effect estimation by pooled stratification: bounded bias and disentanglement) .

###### Proof.

###### Proposition A.2 (One-step correctness) .

###### Proof.

###### Theorem (NES Consistency) .

###### Proof.

##### Residualization (optional).

The theory above uses pooled stratification on $Z_{\texttt{S}}$ with the $\varepsilon$-leakage bound Equation [30](https://arxiv.org/html/2510.14073v1#A1.E30). In practice, one may *arm-wise residualize* the tested coordinate $Z_{j}$ on $Z_{\texttt{S}}$ (e.g., by OLS within each arm) and then apply the same stratified contrast, or use a plain arm difference. This targets the same estimand and can improve finite-sample power, but it is not strictly required.

*Why it helps (variance reduction).* Fix an arm $t$ and consider the $L^{2}(P(\cdot\mid T{=}t))$ projection $R_{j,t}:=Z_{j}-\beta_{t}^{\top}Z_{\texttt{S}}$ with $\beta_{t}=\arg\min_{\beta}\mathbb{E}[(Z_{j}-\beta^{\top}Z_{\texttt{S}})^{2}\mid T{=}t]$. Then

$$ $\mathrm{Var}(R_{j,t}\mid T{=}t)=\min_{\beta}\mathrm{Var}(Z_{j}-\beta^{\top}Z_{\texttt{S}}\mid T{=}t)\ \leq\ \mathrm{Var}(Z_{j}\mid T{=}t).$ $$

Thus, for any stratification weights, the usual Neyman variance for the difference in means built on $R_{j,t}$ is weakly smaller asymptotically than that built on $Z_{j}$ (componentwise, within strata). Intuitively, residualization orthogonalizes $Z_{j}$ against already-discovered codes within arm, removing predictable variation and shrinking the standard error.

*Why it can hurt (finite-sample and misspecification effects).* If $\beta_{t}$ is estimated (say $\hat{\beta}_{t}$) on the same samples used to test $j$, two issues arise:
(i) Estimation noise can inflate variance when S is large or collinear, partially offsetting the variance reduction above.
(ii) Signal leakage in finite samples: although the *population* projection preserves the undiscovered mean contrast under Assumption [A.3](https://arxiv.org/html/2510.14073v1#A1.Thmassumption3), an overfitted $\hat{\beta}_{t}$ can inadvertently subtract some of the undiscovered mean component at $j$ (attenuating the signal and reducing power). Both effects vanish asymptotically if $\hat{\beta}_{t}\to\beta_{t}$.

*Validity and a safe recipe.* If residualization is performed *within arm* and $\beta_{t}$ is estimated on *independent folds* (sample-splitting/cross-fitting), then

$$ $\mathbb{E}[\overline{R}_{j,tg}]\;=\;\mathbb{E}[R_{j,t}\mid G{=}g,do(T{=}t)]+o(1),$ $$

and the Step 2 bounded-bias/cancellation proof applies with $R_{j}$ in place of $Z_{j}$. Hence residualization is asymptotically valid and (typically) more efficient. In small samples without splitting, we still target the same estimand in expectation up to $o_{p}(1)$ under standard regularity, but power can be non-monotone due to estimation noise.

*Recommendation.* We suggest using arm-wise residualization as a complementary efficiency device, with cross-fitting (or estimating $\beta_{t}$ on previously discovered rounds) to avoid overfitting. It cannot worsen asymptotic validity, often improves power by reducing variance, and—implemented with splitting—helps reduce the practical impact of the bounded leakage $\varepsilon$ in Equation [30](https://arxiv.org/html/2510.14073v1#A1.E30).

### Appendix B Neural Effect Test

Figure: Algorithm 2 Neural Effect Test (NET) with stratification on arm-wise residuals

The algorithm tests whether neuron $j$ still carries a *residual* causal contrast after accounting for already–discovered effects S.
We first compute an *arm-wise* residual
$r_{j}:=Z_{j}-\hat{\beta}^{(j)}_{T}{}^{\top}Z_{\texttt{S}}$,
where $\hat{\beta}^{(j)}_{t}$ is fit using only units with $T=t$.
Arm-wise fitting avoids pooled “bad control” on post-treatment codes and cancels leakage from previously found directions as they manifest within each arm.

We then form treatment-agnostic strata $\mathcal{G}$ by coarsening the raw $Z_{\texttt{S}}$ (e.g., medians/quantiles computed *pooled* over $T$) and drop cells lacking both arms.
Within each $g\in\mathcal{G}$ we take the treated–control mean difference of $r_{j}$ and aggregate with weights $w_{g}\propto n_{1g}+n_{0g}$.
This is standardization (g-computation):

$$ $\widehat{\tau}_{j}\;=\;\sum_{g}w_{g}\big(\overline{r}_{j,1g}-\overline{r}_{j,0g}\big)\;\xrightarrow{\ \mathbb{E}\ }\;\sum_{g}\Pr(G{=}g)\!\left(\mathbb{E}[r_{j}\mid G,g,do(1)]-\mathbb{E}[r_{j}\mid G,g,do(0)]\right)=\tau^{R}_{j},$ $$

so the estimator is unbiased under randomization/SUTVA. The reported variance and Satterthwaite df are the usual stratified formulas.

### Appendix C Minimal Python Implementation Snippet

We provide a minimal Python snippet for our algorithm relying on pandas library [McKinney et al., 2011] for tabular operations and SciPy library for statistical testing [Virtanen et al., 2020] .

##### Neural Effect Search

Recursive discovery.

##### Neural effect Test

By stratification with median binning. For simplicity we ignore here arm-wise residualization (see full code for detailed implementation).

### Appendix D Experiments Details

#### D.1 CelebA semi-synthetic RCTs

Dataset.
We use CelebA [Liu et al., 2018], a face attributes dataset with $>200\mathrm{k}$ images and $40$ binary attributes per image (^2^22It can be downloaded from [flwrlabs/celeba](https://huggingface.co/datasets/flwrlabs/celeba)). Furthermore, for implementation details, labels have been doubled (we pass from Beard to Has_Beard and Has_notBeard). We follow the authors’ official *train/val/test* split, and we employ the validation data for training SAEs and the test data to interpret them. Attributes are treated as ground-truth binary labels. From this source, we simulate several RCTs following the data generating process (DGP) described below, varying the sample size ($n\ll 200k$) and treatment effect ($\tau$), reflecting realistic randomized controlled trial characteristics.

Data Generating Processes
To evaluate discovery accuracy with known ground truth, we simulate RCTs by reusing real images but stochastically sampling treatment and outcomes from CelebA attributes:

- •
Treatment: $T\sim\mathrm{Bernoulli}(0.5)$.
- •
Outcome factors: we designate two binary effects $Y{=}(Y_{1},Y_{2})$ using CelebA attributes: $Y_{1}{=}\texttt{Eyeglasses}$, $Y_{2}{=}\texttt{Wearing_Hat}$.
- •
Exogenous Cause: $W{=}\texttt{Smiling}$.

We implement a “co-effect” model in which $T$ shifts both $Y_{1}$ and $Y_{2}$ with arm-specific probabilities and $W$ modifies only $Y_{1}$:

$$ $\displaystyle\Pr(Y_{2}{=}1\mid T{=}1)=p^{(Z)}_{1},\quad\Pr(Y_{2}{=}1\mid T{=}0)=p^{(Z)}_{0},$ $\displaystyle\Pr(Y_{1}{=}1\mid T{=}t,W{=}w)=$ $$

with $W\sim\mathrm{Bernoulli}(0.5)$. We vary effect magnitude via an ATE grid $\mathrm{ATE}\in\{0,0.1,\dots,0.8\}$ (9 values). Concretely, starting from a base rate $0.5$, we set:

$$ $p^{(Z)}_{1}=0.5+\tfrac{\mathrm{ATE}}{2},\quad p^{(Z)}_{0}=0.5-\tfrac{\mathrm{ATE}}{2},$ $$

and analogously for $Y_{1}$ in the $W{=}1$ arm:

$$ $p^{(Y)}_{11}=0.5+\tfrac{\mathrm{ATE}}{2},\quad p^{(Y)}_{01}=0.5-\tfrac{\mathrm{ATE}}{2},\quad p^{(Y)}_{10}=0.2+\mathrm{ATE},\quad p^{(Y)}_{00}=0.2.$ $$

For each simulated unit, we draw $(T,W,Y_{1},Y_{2})$, then assign an *actual image* whose CelebA attributes match the realized $(Y_{1},Y_{2},W)$.

FM features.
Each image $x$ is encoded with SigLIP [Zhai et al., 2023] into a patch-level representation; we use the final-layer token features (dim $d{=}768$, $196$ patches/token positions). Unless noted otherwise, we do not use any task-specific fine-tuning.

SAE Details.
We train a SAE on SigLIP features to obtain interpretable codes $Z\!\in\!\mathbb{R}^{m}$ that serve as hypotheses for treatment effect estimation. Thereafter, the details for the SAE in Table [1](https://arxiv.org/html/2510.14073v1#A4.T1). Lastly, to turn hidden representation into hypotheses, aggregate patchwise by *mean pooling* to a single $Z\in\mathbb{R}^{9216}$ per image. These per-image codes are the units we test in NES and baseline procedures.

**Table 1: Training details for the SAE employed in semi-synthetic experiments.**
| Component | Setting |
| --- | --- |
| Encoder nonlinearity | Top-$k$ with $k{=}5$ active codes |
| Input dimension | $768$ |
| Code / decoder dimension ($m$) | $9216$ |
| Optimizer / LR / batch | Adam / $5{\times}10^{-4}$ / $20$ |
| Epochs / grad clipping | $20$ / $1.0$ |

##### Evaluation.

We evaluate discoveries against concept–aligned SAE codes extracted from CelebA. Let $m{=}9216$ be the number of codes and $Z_{j}(X)\in\mathbb{R}$ the activation of code $j\in[m]$ on image $X$; a code is *active* when $Z_{j}(X)>0$. For true effect $Y_{k}\in\{0,1\}$ (here $k\in\{1,2\}$) and each code $j$, we induce predictions $\hat{y}^{(j)}_{ik}\mathrel{\mathop{:}}=\mathbb{I}\{Z_{j}(X_{i})>0\}$ and compute the F1-score of $\{\hat{y}^{(j)}_{ik}\}_{i=1}^{n}$ against the ground-truth labels $\{y_{ik}\}_{i=1}^{n}$; the *best* neuron for the concept is then

$$ $g_{k}\;\mathrel{\mathop{:}}=\;\arg\max_{j\in[m]}\ \mathrm{F1}\!\left(\{\hat{y}^{(j)}_{ik}\}_{i=1}^{n},\ \{y_{ik}\}_{i=1}^{n}\right).$ $$

The resulting ground-truth set of affected codes is $\mathcal{G}\mathrel{\mathop{:}}=\{g_{1},g_{2}\}$ (in general $|\mathcal{G}|=r$). Each method (NES or a baseline) returns a set of discovered codes $\mathcal{S}\subseteq[m]$, which we compare to $\mathcal{G}$ via set metrics. Defining $\mathrm{TP}\mathrel{\mathop{:}}=|\mathcal{S}\cap\mathcal{G}|$, $\mathrm{FP}\mathrel{\mathop{:}}=|\mathcal{S}\setminus\mathcal{G}|$, and $\mathrm{FN}\mathrel{\mathop{:}}=|\mathcal{G}\setminus\mathcal{S}|$, we report

$$ $\mathrm{Precision}\;=\;\frac{\mathrm{TP}}{\mathrm{TP}+\mathrm{FP}},\qquad\mathrm{Recall}\;=\;\frac{\mathrm{TP}}{\mathrm{TP}+\mathrm{FN}},\qquad\mathrm{F1}\;=\;\frac{2\,\mathrm{Precision}\cdot\mathrm{Recall}}{\mathrm{Precision}+\mathrm{Recall}},$ $$

and the set Intersection-over-Union (IoU)

$$ $\mathrm{IoU}\;=\;\frac{|\mathcal{S}\cap\mathcal{G}|}{|\mathcal{S}\cup\mathcal{G}|}\;=\;\frac{\mathrm{TP}}{\mathrm{TP}+\mathrm{FP}+\mathrm{FN}}\,.$ $$

#### D.2 ISTAnt

##### Data and RCT.

We considered the randomized controlled trial introduced by Cadei et al. [2024]. Videos of ant triplets were collected under randomized treatment/control assignment. Throughout our unsupervised pipeline, *domain annotations from biologists were used only a posteriori for interpretation/evaluation of discovered codes, never for training*, as discussed in the main text.

FM features.
Each frame $X$ is encoded with DINOv2 [Oquab et al., 2023] into a patch-level representation; we use the final-layer token features (dim $d{=}384$, $256$ patches/token positions). Unless noted otherwise, we do not use any task-specific fine-tuning.

SAE Details.
We train a SAE on the DINOv2 features to obtain interpretable codes $Z\!\in\!\mathbb{R}^{m}$ that serve as hypotheses for treatment effect estimation. Thereafter, the details for the SAE are in Table [2](https://arxiv.org/html/2510.14073v1#A4.T2). Lastly, to turn hidden representation into hypotheses, we aggregate patchwise by *mean pooling* to a single $Z\in\mathbb{R}^{4608}$ per frame. These per-frame codes are the units we test in NES and baseline procedures.

**Table 2: Training details for the SAE employed on ISTAnt.**
| Component | Setting (ISTAnt) |
| --- | --- |
| Encoder nonlinearity | Top-$K$ with $K{=}20$ active codes |
| Input dimension | $384$ |
| Code / decoder dimension ($m$) | $4608$ |
| Optimizer / LR / batch | Adam / $5{\times}10^{-4}$ / $128$ |
| Epochs / grad clipping | $10$ / $1.0$ |

##### Evaluation.

Evaluation follows exactly the CelebA protocol: we score discovered codes against ground-truth concepts via code–induced predictions and compute Precision/Recall/F1 and IoU for the set of returned codes (with domain annotations used only for interpreting and quantifying performance, not for training).

### Appendix E Additional Experiments

#### E.1 Evaluation on CelebA : what does our ground truth model?

We assess how well SAE codes behave as measurement channels on CelebA by aligning individual neurons with ground–truth attributes (see Section [D.1](https://arxiv.org/html/2510.14073v1#A4.SS1)). For each code $j$, we treat the event $Z_{j}>0$ as a binary predictor and compute its F1–score against the attribute label. The two most predictive neurons for the two affected factors are:
(i) neuron 38 for Wearing_Hat with $\mathrm{F1}=0.841$, and (ii) neuron 6051 for Eyeglasses with $\mathrm{F1}=0.748$.
Qualitative inspection of the top–activated images (Figure [6](https://arxiv.org/html/2510.14073v1#A5.F6)) confirms that these codes fire on the intended visual concept, supporting their use for exploratory causal inference.

Figure: Figure 6: Qualitative neurons’ interpretations. Each panel shows the 12 most–activated test images for the most predictive neuron of each affected outcome concept (activation = highest code value).
Refer to caption: x5.png

At the same time, the F1–score spectra over *all* neurons reveal a familiar pattern: a single, dominant “monosemantic” code per concept, accompanied by a long tail of weaker yet clearly non–zero correlations (Figure [7](https://arxiv.org/html/2510.14073v1#A5.F7)). This tail is stronger for Eyeglasses, where several neurons reach moderate F1, indicating broader leakage/entanglement. As discussed in the main text (see Section [3](https://arxiv.org/html/2510.14073v1#S3)), such low–amplitude but widespread correlations are precisely what trigger the *Paradox of Exploratory Causal Inference*: with enough power, standard multi–testing will flag all of these leakage neurons as “significant.” Our NES counters this by retrieving the leading effect first and then recursively stratifying on previously discovered codes, so that subsequent tests target the *residual* causal signal rather than its leakage.

Figure: Figure 7: Monosemantic peaks with entanglement tails. For each attribute, we rank SAE codes by F1 against the CelebA label and visualize the top performers in order.
Refer to caption: x6.png

#### E.2 In–depth analysis: full semi–synthetic results

This subsection expands the quantitative picture in Figure [4](https://arxiv.org/html/2510.14073v1#S6.F4) by showing the *more complete grid* of results across sample size and effect magnitude, for two evaluation regimes:

- 1.
Unknown number of effects ($r$). Each method returns its *own* set of significant codes at level $\alpha$ or simply the Top-K. We then report Precision, Recall, and IoU against the ground–truth affected codes (Section [D.1](https://arxiv.org/html/2510.14073v1#A4.SS1)).
- 2.
Known number of effects ($r$). We assume to know the true number of effects, and we just look at $r-$ highest effect among each method. We again compute Precision, Recall, and IoU (namely, we apply Top-2 selection on top of other methods).

As detailed in Appendix [D.1](https://arxiv.org/html/2510.14073v1#A4.SS1), we vary (*i*) the sample size $n\in\{30,50,100,250,500,1000\}$ and (*ii*) the ATE magnitude $\tau\in\{0.1,\dots,0.8\}$, holding the semi–synthetic DGP and SAE training protocol fixed. Each cell aggregates 10 random seeds (RCT re–draws and SAE initializations).

##### Main takeaways.

Across both regimes and over the entire grid, NES maintains high Precision and IoU while matching the best Recall of baselines. When the experiment power increases (larger $n$ or $\tau$), vanilla $t$–tests and classical multiplicity corrections (FDR/Bonferroni) exhibit the *significance–collapse* behavior: Recall saturates but Precision drops sharply as leakage neurons become significant, driving IoU toward zero. Enforcing the correct cardinality ($r$ known) mitigates over–selection but does *not* resolve entanglement: baselines still replace a true effect with a leakage surrogate in later picks, keeping Precision $<\!0.5$ in the high–power regime. In contrast, NES’s residual stratification peels one principal effect component per round and then *stops*, preserving interpretability.

Figure: Figure 8: Full results with $\bm{r}$ unknown. Precision, Recall, and IoU for all methods when each returns its own set of significant codes at level $\alpha$$=0.05$.
Refer to caption: x7.png

Figure: Figure 9: Full results with $\bm{r}$ known (top–$\bm{r}$ selection). Precision, Recall, and IoU when every method is forced to return exactly $r$ codes (the true number of effects).
Refer to caption: x8.png

#### E.3 Ablation I: No Causal Effect

We repeat the semi-synthetic evaluation of Section [E.2](https://arxiv.org/html/2510.14073v1#A5.SS2) but set the true ATE to zero, namely $\tau=0$ factors. In this regime, a well-calibrated discovery procedure should return *no* significant neurons.

Figure: Figure 10: Zero-effect ablation . Number of discovered neurons by method when ATE is 0.
Refer to caption: x9.png

We keep the data-generating process, foundation model, SAE training, and testing grid over sample sizes $n$ identical to Section  [E.2](https://arxiv.org/html/2510.14073v1#A5.SS2), changing only the interventional contrast to $\mathrm{ATE}=0$. For each method, we record the number of discoveries per run. Across all sample sizes, NES returns an empty set: in the first iteration, no neuron survives Bonferroni at level $\alpha/m$, and the recursion halts. Furthermore, both Bonferroni and FDR also yield essentially zero discoveries. In contrast, the uncorrected $t$-test produces spurious positives (false discoveries), and Top-$k$ necessarily reports $k$ indices by design, labeling pure noise as significant. This behavior matches our theoretical intuition: with $\tau=0$ there is no effect vector to leak into entangled coordinates, so the paradox of Sec. [3](https://arxiv.org/html/2510.14073v1#S3) does not arise; procedures that control multiplicity (NES via its first-step Bonferroni gate, Bonferroni, and FDR) appropriately abstain, whereas selection rules that ignore multiplicity (Top-$k$, plain $t$-tests) over-discover.

#### E.4 Ablation II: Testing in NES

We compare three per-round gates inside NES (Alg. [1](https://arxiv.org/html/2510.14073v1#alg1)): Bonferroni, FDR, and $t$-test. Same setup as Sec. [E.2](https://arxiv.org/html/2510.14073v1#A5.SS2); only the multiplicity rule changes while recursion and residual stratification are unchanged. *NES-Bonf.* delivers the cleanest recoveries: highest precision/IoU and exact stopping at $r$ effects when powered; under $\mathrm{ATE}{=}0$ it returns none (cf. Ablation [E.3](https://arxiv.org/html/2510.14073v1#A5.SS3)). *NES-$t$* is most exploratory for small sample size and effect magnitude but over-selects as power grows, i.e., Paradox of Exploratory Causal Inference.

Recommendation. Prefer a multi-hypothesis testing correction, i.e., Bonferroni/FDR, when the power of the experiment is high, while consider $t$-test for a more explorative approach in low power regime.

Figure: Figure 11: Testing in NES. Bonferroni: best precision/IoU and exact stopping; FDR: higher sensitivity in low power, minor over-selection; $t$-test: exploratory but prone to over-discovery as power increases.
Refer to caption: x10.png

#### E.5 Ablation III: AIPW vs. Associational Difference

Throughout the paper, our per-neuron hypothesis test uses the *associational difference* (AD), i.e., a two-sample $t$-test on the treated–control difference in means. In randomized trials, AD is unbiased for the ATE, but it is not semiparametrically efficient. A standard variance–reduction alternative is *Augmented Inverse Propensity Weighting* (AIPW; Robins et al., 1994), which orthogonalizes the estimator against misspecification of either the propensity score or the outcome regression.

##### Setup.

For each code $j$, let $Z_{ij}$ be its activation for unit $i$, $T_{i}\!\in\!\{0,1\}$ the treatment, and $W_{i}$ observed exogenous causes. We compute the AIPW pseudo-outcome

$$ $\tilde{Z}_{ij}\;=\;\hat{\mu}_{1j}(W_{i})-\hat{\mu}_{0j}(W_{i})\;+\;\frac{T_{i}}{\pi(W_{i})}\big(Z_{ij}-\hat{\mu}_{1j}(W_{i})\big)\;-\;\frac{1-T_{i}}{1-\pi(W_{i})}\big(Z_{ij}-\hat{\mu}_{0j}(W_{i})\big),$ (36) $$

where $\pi(W)\!=\!\Pr(T\!=\!1\mid W)$ (known and constant $\pi=0.5$ in our RCT), and $\hat{\mu}_{tj}(W)\approx\mathbb{E}[Z_{j}\mid T\!=\!t,W]$ is a nuisance regression. The AIPW estimate of the code-level ATE is $\hat{\tau}^{\text{AIPW}}_{j}=\frac{1}{n}\sum_{i}\tilde{Z}_{ij}$; we test $H_{0}:\tau_{j}=0$ via a one-sample $t$-test on $\{\tilde{Z}_{ij}\}_{i}$ with robust variance.

##### Results.

Figure [12](https://arxiv.org/html/2510.14073v1#A5.F12) compares AD vs. AIPW on the semi-synthetic benchmark across sample size $n$ and effect magnitude $\tau$.
In our setting—with a truly randomized treatment ($\pi=0.5$) and a *single* binary covariate $W$—AIPW yields only marginal efficiency gains: Precision/Recall/IoU curves are essentially overlapping, with small stability improvements for AIPW at the smallest $n$.
Crucially, orthogonalization affects variance but *does not* resolve entanglement: the significance–collapse phenomenon for standard multi-testing (Section [3](https://arxiv.org/html/2510.14073v1#S3)) persists under AIPW, and NES retains its advantage because its benefit comes from recursive stratification (disentangling residual effects), not from how the first-step mean contrast is estimated.

##### Takeaways.

(i) In pure RCTs with weak, low-dimensional $W$, AD is competitive and simpler. (ii) AIPW can be preferred when richer exogenous information is available (higher-dimensional $W$, imbalance, or mild protocol deviations), where its variance reduction can translate into earlier detection of the leading effect; (iii) regardless of AD or AIPW, NES’s stratified recursion is the key to avoiding over-discovery under entanglement.

Figure: Figure 12: AIPW vs. AD on semi-synthetic RCTs. Precision, Recall, and IoU when replacing the per-neuron associational difference (AD) with AIPW (Eq. [36](https://arxiv.org/html/2510.14073v1#A5.E36)) for baselines and the first NES step.
Refer to caption: x11.png

## Peer Reviews

confidence: 3
contribution: 2
initial_rating: 4
presentation: 2
questions: 6. Is the proposed method restricted to experimental settings in which $T$ is being intervened? Or could it also be applicable in general cases in observational studies such as where $T$ is interpreted as an instrumental variable?

7. Why is it necessary to remap $X$ to a representation from the foundation model?

8. What makes the idea of learning the outcomes different from papers that study causal disentangled representation learning? Is it the idea that outcomes are different from other variables? Why so?
soundness: 3
strengths: 1. A method of performing experimental studies that is not inherently biased by a predetermined hypothesis can be quite useful. The idea of learning targets instead of having a preestablished one is a novel concept.

2. Experiments provide some interesting insight into the consequences of the proposed approach.
summary: The paper aims to discover treatment effects on targets that are unknown. As opposed to prediction-powered causal inference, in which the goal is to perform experiments to study hypotheses on known targets, the paper focuses on exploratory causal inference, where the targets are discovered from data, and causal effects are interpreted afterwards. The proposed approach first obtains representations of measurements through a pretrained foundation model and then reparameterizes them using a sparse autoencoder. Results are provided that state that the resulting variables are entangled, and they are processed through a procedure called Neural Effect Search to produce a set of disentangled variables.
weaknesses: 3. The problem does not seem very well-defined from the perspective of variable definitions. Notably, it is unclear what makes something an outcome (part of $Y$) or a measurement (part of $X$). Especially if in this problem setting, $Y$ is constructed by processing $X$ deterministically, statistical independence tests (e.g., to check if $T \perp X \mid Y$) are potentially invalid due to lack of positivity.

4. Guarantees of the proposed approach are mostly leveraging mutual information between variables, but mutual information may not capture causal nuances between variables.

5. The paper could be improved in clarity. Notably, it might help to include a figure of the whole pipeline or perhaps an example.

---

confidence: 4
contribution: 3
initial_rating: 8
presentation: 3
questions: **Q: Computing** v_k **when** Y **is unobserved.**

In eq.4 you define the “neuron effect” vector for factor Y_k as $v_k := \mu(Y_k{=}1)-\mu(Y_k{=}0)$, which you later use for NES. However, in your main RCT setting the semantic factors Y=(Y_1,\dots,Y_r) are not observed. Could you clarify how v_k is computed in practice?
soundness: 3
strengths: The paper is very well-written with clear problem framing and clear methodology paired with real-world case study. It is a promising work for exploratory science workflows.
summary: The paper proposes an exploratory causal inference pipeline for RCTs with unstructured/high-dimensional outcomes. The main contribution is Neural Effect Search and its application on real experimental ecology trial.
weaknesses: Relation to variable selection. Since NES aims to identify which SAE codes carry treatment effects, could you compare it against classical variable-selection baselines for effect modifiers? E.g., Lasso with group/hierarchical penalties, knockoffs or stability selection for support recovery. Such comparison may clarify what NES adds beyond standard selection.

---

confidence: 2
contribution: 4
initial_rating: 8
presentation: 2
questions: On line 143, what does it mean to "assume T is not directly visible in X".  For example, thinking of the ant grooming example where the treatment is some substance that the ants were given, does this just mean that none of the substance is directly seen in any of the pixels of the images?  If so, how does this map to a "double-blind randomized trial"? (if T not being directly visible in X just means something like not seeing the substance pixels in the image, that doesn't seem to relate to whether or not the ants taking the substance knew that they took it or not)

When discussing Figure 2 (center) in the middle of page 3, this seems to be strongly related to work by Cadei et al., 2024 and 2025.  However, in that 2024 paper, there's a similar, but different, causal structure (Figure 1 in that paper) that seems to describe the same problem where we only observe a high-dimensional observation view of the outcome of interest.  Rather than X being caused by W and Y (as in Figure 2 (center)), they have X being caused by T and W and then causing Y.  Can you explain the reason for this difference, despite the problem settings, at least superficially, seeming very similar?

On line 158, when talking about Figure 2 (right), you state that you have T being independent of W given Y.  However, that doesn't appear to be true in Figure 2 (right) - it looks like conditioning on Y, which is a collider between T and W, would induce dependence.

I feel like I'm missing something about the title.  I get that your approach uses SAEs, and it looks like some sort of play on "seance", but "SAEnce" doesn't appear to be the name of your algorithm (which is NES), and you never refer to the term "SAEnce" in the paper.
soundness: 3
strengths: Overall, I think the this is a great paper.  The problem definition, though hard to understand initially, is novel and compelling.  The authors make a solid case about the value of empirical exploratory causal inference, and their approach seems well-reasoned.  Apart from the issue of the problem statement needing more upfront description/examples, the rest of the paper is well-presented, and the writing is clear and easy to follow.  For an approach to solving a problem that hasn't been studied much before, I think the authors did a good job at still doing a reasonable evaluation.  I also appreciate the authors' scientific rigor with respect to the dangers of multiple hypothesis testing and the need for a human analyst.
summary: The authors focus on an empiricist, rather than rationalist, approach to analyzing data from RCTs.  The increase in large data collections opens up a increasing range of datasets where interventions were performed without clear hypotheses or outcome targets.  In such domains, it can be useful to explore the space of possible outcomes for a given treatment, but the high dimensionality of the observation space can make disentangling concrete outcomes challenging and can lead to the detection of large numbers of spurious correlations if care isn't taken.  To tackle these challenges, the authors propose a new procedure that extracts a representation from the input data using a foundation model, applies a sparse autoencoder to separate out atomic outcomes.  However, these dimensions may still be strongly entangled.  The authors account for this with an algorithm they propose, NES, that recursively identifies and removes outcomes from the SAE representation, resulting in a set of possible outcomes that can be interpreted by an analyst.  The authors explain how this procedure can be implemented and how it avoids issues around multiple hypothesis testing, and evaluate its performance with semi-synthetic and empirical datasets.
weaknesses: While I generally think the central idea of this paper is strong, the presentation is the weakest part.  The problem definition the authors are working with (RCTs without a directly measured, or even defined, outcome) is interesting but very uncommon in the literature, and the authors' description of it in the paper is insufficient.  The setting seems to be the same as that used in Cadei et al. 2024 and 2025, and it was only through reading the examples in those papers that I was able to really understand the problem domain.

The first part that this lack of sufficient explanation hit for me was at the top of page 2, where the authors state that "Clearly, [understanding the spread of disease from fine-grained social interactions] can be dramatically accelerated with computer vision, using the predictions of a model as input for causal inference pipelines (Cadei et al, 2025)."  Without following the reference, this is the first time "computer vision" or images are brought up, so the "clearly" definitely doesn't work for the reader here.  Similarly, the following sentence about deciding what to annotate is equally unclear when the authors haven't yet given us the framing of the problem as one where outcomes must be inferred from pixels in images.  The authors then, in line 64, mention that the problem they consider is RCTs where the effect is measured indirectly, possibly through imaging.  However, the concept of an RCT without an explicitly measured outcome is counterintuitive in most domains.  When we eventually get details about the ant grooming example, it makes sense and is a compelling problem definition, but until then, the problem statement remains incredibly murky.

My recommendation would be to put the ant grooming example in the introduction.  Even with the brief discussion of the ant grooming problem in this paper (first around like 146, and then again in the experiment section), the details are very light, and it wasn't until I read the first two sections of Cadei et al. 2024 that that data set (and thus your problem definition ) really became clear to me.  I think the main piece that was missing from this paper is why outcomes wouldn't be directly observable in an RCT.  Giving a concrete example and explaining that an outcome could be, for example, a specific type of ant grooming behavior (which can only be inferred by an expert watching the frames of a video) would make the paper much easier to follow.  And then you can easily explain that, while in some cases experts may have specific behavior they're expecting to change upon treatment, this may cause them to miss other interesting behaviors that are also inferable from the video.  Through the rest of the paper, there are other parts that seem like they would benefit from example, so having a running example set up early on would help a lot. (e.g., on page 3, when discussing Figure 2 center and right)

The experiments are interesting and well-done.  However, I wish the authors had actually described what the "palette background" effect was in the ISTAnt experiment.  Even just putting it in the appendix would help.  As-is, needing to go to another paper to even understand the empirical evaluation isn't ideal.  I'm not really even sure what the description on line 430 means ("top right black color mark in the top left position in the first 4 batches of videos") - in the bottom row of Figure 5, I do see black marks in the top right of the first two images, but I'm not sure what "the top left position" means there.

I guess this doesn't really diminish the contribution, but it's very odd to have what looks like an algorithm name in the title of your paper (SAEnce) but then not actually have that be the algorithm name (NES).  From Figure 1, I assumed that NES was just part of an overall procedure called SAEnce, but then you never actually use the term SAEnce outside the title.

While not rampant, there are some grammatical issues that could be cleaned up.  These didn't affect my score, but just for your information, here are some that I noted early on:
- line 43: "or more in general" -> "or more **generally**"
- line 46: "modern science started embracing the creation of atlases" -> "modern science **has started embracing the creation of atlases**
- line 48: "(Weinstein et al., 2013), imaging of cells ..." -> "(Weinstein et al., 2013), **and** imaging of cells ..."
- line 72: "One effect after the other" doesn't fit at the end of that sentence.  You at least need a comma before it (and really, I think it would sound better with a verb, but I'm not quite sure what would fit best - maybe "**, extracting** one effect after the other"?)
- line 127: I think "i.e., T has no causes" should be in parentheses

---

confidence: 4
contribution: 3
initial_rating: 8
presentation: 3
questions: 1.	Can you characterize the overall FWER/FDR of the entire recursive NES (not just within-round Bonferroni)? Any feasible post-selection correction or stability-selection variant?
2.	What quantitative leakage/entanglement metrics do you compute pre- and post-NES? Can you report these alongside effect discoveries to guide practitioners? E.g., your leakage set/index definition as a reported diagnostic.
3.	How stable are discovered effects across different FMs (e.g., DINOv2 vs. CLIP/SigLIP), code sizes, sparsity penalties, and random seeds? Any consensus-NES idea where you intersect effects across runs?
4.	In the ecology study, could you provide bootstrap confidence intervals for NES effect sizes on residualized codes, or permutation tests that respect the randomization?
5.	Beyond “stop when no rejections,” is there any data-dependent stopping that protects against over-peeling? And for multiple effects, how robust is the ordering (largest first) under moderate entanglement?
6.	Could NES results predict downstream manual labels or behavioral rates on an unseen experimental batch, thereby validating discovered effects?
soundness: 3
strengths: Originality. The manuscript frames an under-explored empiricist alternative to “prediction-powered” causal inference by discovering what was affected (unknown $Y$) rather than who is affected (heterogeneity over $W$). The formal paradox and its asymptotics represent a crisp conceptual advance that explains why usual multi-testing fails under entanglement.

Quality. The NES procedure is simple, causally motivated (conditioning/stratification to remove leakage and collider bias), and backed by a consistency theorem under a clear SCM. The proofs (appendix) show how arm-wise residualization preserves the remaining causal contrasts. 

Clarity. Pipeline and problem setting are clearly contrasted with classical RCTs and “prediction-powered” approaches. Figures and toy examples clearly communicate the paradox and the proposed fix.
 
Significance. If validated more broadly, NES could become a practical hypothesis-generation and pruning layer for large, instrumented experiments (biology, ecology, imaging, etc.), reducing annotation burden while keeping statistical guardrails. The empirical ecology case shows it can recover a known behavior (grooming) and also surface a background artifact that informs experimental redesign.
summary: The paper proposes Exploratory Causal Inference. Starting from raw, high-dimensional measurements $X$ collected in randomized trials where the specific outcome variables $Y$ are unknown, the authors extract representations with a foundation model (FM), reparameterize them with a sparse autoencoder (SAE), and then test for treatment effects at the level of SAE codes. They identify a core failure mode, the paradox of exploratory causal inference, where classical multiple testing (even with Bonferroni/FDR) flags all entangled neurons as “significant” as sample size or effect size grows, destroying interpretability. To address this, they introduce Neural Effect Search (NES), a recursive, arm-wise residual stratification procedure that peels away effects one by one and (under assumptions) consistently recovers the true effect subspace. They present semi-synthetic experiments (CelebA-based) and a real randomized ecology trial (ISTAnt ants) where NES identifies a behavior (grooming) and a nuisance/background correlate.
weaknesses: Identification hinges on SAE/FM assumptions. Consistency requires that the true effect directions live (approximately linearly) in the SAE code space and that the SAE reaches a sufficiently mono-semantic regime. This is acknowledged as the biggest limitation in the manuscript. The paper would benefit from stress tests across different FM/SAE choices, sparsity regimes, and code dimensionalities, plus diagnostics for “are we in a regime where NES is trustworthy?” (e.g., leakage indices before/after NES and stability under code re-initialization). 

NES uses Bonferroni within rounds, but the recursion adaptively selects and conditions on previous picks. The theorem covers recovery of directions under asymptotics. However, finite-sample error rates (FWER/FDR) across the entire procedure remain unclear. The authors are suggested to quantify family-wise error or provide a selective-inference style bound for the full recursion (or a practical stopping rule tied to post-selection adjusted p-values). 

The toy setups are helpful but narrow. The authors may consider adding settings with (i) multiple effects with very different magnitudes; (ii) nonlinear superposition in codes; (iii) batch effects and arm imbalance; (iv) mis-specified FMs (domain shift). It would be helpful to report precision/recall/IoU when ground-truth effects are weak and overlapping, and ablate stratification choices.

The real trial yields two neurons; one aligns with grooming ($F1\approx0.40$), another with palette background correlated with treatment due to small $n$. This convincingly demonstrates hypothesis surfacing, but decisions based on neural codes remain risky. Strengthen the case with expert-verified labeling for the surfaced codes (beyond top clips), pre-registered confirmatory tests, or a hold-out colony/day to show replicability.


Decision: Accept (Oral)