Exploratory Causal Inference in SAEnce
Authors: Tommaso Mencattini
Riccardo Cadei
Francesco Locatello
Venue: ICLR 2026 Oral (2026)
Keywords: Randomized Controlled Trials
Sparse Auto Encoder
Interpretability
Causal Inference
Primary area: interpretability and explainable AI
TL;DR: New method to uncover causal treatment effects directly from trial data using foundation models, SAE and recursive stratification, without any prior and supervision.

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 Auto Encoder. 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.

Published as a conference paper at ICLR 2026
EXPLORATORY CAUSAL INFERENCE IN SAENCE
Tommaso Mencattinit.12 Riccardo Cadeit.l, Francesco Locatello
Institute of Science and Technology, Austria (ISTA) École Polytechnique Fédérale de Lausanne (EPFL)
i Equal contribution.
ABSTRACT
Randomized Controlled Trials are one the pillars science; nevertheless, they rely hand-crafted hypotheses and expensive analysis. Such constraints prevent causal effect estimation at scale, potentially anchoring on popular yet incomplete hypotheses. We propose discover the unknown effects of 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-testin 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 robustmess of our algorithm on semi-synthetic experiments, we showcase, in the context of experimental ecology, the first successful unsupervised causal effect identification real-world scientific trial.
i. experiment
i. represent
select
iv. interpret A
Sokect PNCUOOES
Mic fug coniccpds
FM
SAE
M2
M;
TOC Ag partfoe
Figure I: Pipeline for Exploratory Causal Inference: (i) collect experimental data, (ii) extract in- terpretable representations via a Foundation Model and Sparse Autoencoder, (iii) identify treatment effects, e.g., via Neural Effect Search, and (iv) interpret the causal findings, i.e., affected neurons.
INTRODUCTION
In science, data has been historically collected to answer specific questions (Popper 2005). In this rationalist view, scientists formulate hypothesis, often causal query, and collect data to falsify it. For example, experimental ecologists studying social immunity in ants (Cremer et al.) 2007 may suspect that exposure specific micro-particle may affect specific social behaviors, or more formally, "a treatment T has a causal effect on an outcome behavior Y". They then perform controlled experiment, administering the treatment or placebo sample of individuals and check whether there is significant difference in the correlation between the treatment assignment and the outcome. While this paradigm has dominated science for centuries, modern science has 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), and imaging of cells under thousands of perturbations (Sypetkowski et al. 2023) to name a few. Different than the classical paradigm, these datasets call for empiricist view, starting with exploratory data-driven investigations. The new challenge is that the immense size of these datasets prohibits scientists from simply "looking the data and finding what is interesting". Even beyond atlases, in

---

Published as a conference paper at ICLR 2026
motivating example from experimental ecology, fine-grained social interactions between many individuals are complex yet critical for understanding the spread of a disease (Finn et al. 2019). Hopefully, data processing relying on pre-trained foundational models and leveraging artificial predictions within causal inference pipelines (Cadei et al. (025). Still, scientists need to decide what "look at" a-priori before to validly annotate the data and infer causal relationships, potentially biasing the analyses towards recurrently studied behaviors, phenomena known as the "Matthew effeet" (Merton 1968) or informally as "rich-ged rech-get-richer.: scientists are biased by prior successful investigations.
be dramatically accelerated with modern machine learning, e.g.,
Motivating Example: behavioral effects Social Immunity research
Experimental ecologists collect video data of ants' interactions under different treatments to study social immunity policies man- ifested specific behaviors (Cremer et al.) 2007: Cadei al. 2024). In practice, these behaviors are not directly measured, but annotated from the videos by hand or using machine learning.
Which behaviors to study is determined by the scientists' prior
(not data driven), which may not be priori clear or exhaustive in exploratory experiments.
In this paper, we characterize differences and synergies between the classical rationalist view and the emerging empiricist one and propose a method identify statistically significant effects in ex- ploratory experiments, formally grounding it with the language of statistical causality, see Figure We formulate the problem on experimental data, where a treatment is administered randomly and the possible effects are measured indirectly, c.g., imaging or other raw observations. Instead of requiring scientists to formulate treatment effect hypotheses, label some data, and train a model to propose to train a sparse autoencoder (SAE) on the representation of a foundation model and generate data-driven effect hypotheses interpreting the significant effects the neural representations (i.e., empiricist approach). In this new paradigm, the main challenge is that, if the SAE is not perfectly disentangled (Elhage al. 20022), any neuron minimally entangled with the true effect may appear significantly treatment-responsinn challenging the results interpretation. To address it, we propose a novel recursive stratification technique iteratively correct the effect on entangled neurons.
extend labels the whole dataset (i.e., the rationalist view (Cadei et al. 2024 2025)
Looking at the data before committing to any hypothesis, we overcome the Matthew effect, enrich- ing the rationalist view a data-driven way. We propose work with pretrained foundation models, training SAEs directly on the target experimental data. This is important because pretrained foun- dation models can be biased as well, which is problematic for drawing scientific conclusions (Cadei et al. 2024). Instead of directly testing single hypothesis. our approach enables to preliminary explore thousands potential effects in a semantically expressive latent space, still allowing the domain experts to interpret, judge and eventually test them posteriori. This is in stark contrast with preliminary empiricist approaches in causality like "causal feature learning" (Chalupka et al. 2017). which only commits to single hypothesis by discrete clustering. Our contributions
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 autoen- coders. We characterize the statistical challenges in multiple hypothesis testing discover treat- ment effects over neural representations in the paradox of exploratory causal inference (ours). Then, we introduce Neural Effect Search, a novel iterative hypothesis testing procedure over- come such challenges.
We showcase in both semi- mmmi-synthetic (real images with controlled causal relations) and a worl-world trial in experimental ecology that approach is capable of identifying the treatment effects in a exploratory experiment. To the best of our knowledge, this is the first successful application of sparse autoencoders causal inference, tailored to the analysis of scientific experiments.
2

---

Published as a conference paper at ICLR 2026
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 as upper-case, boldface letters.
W
W
T
Y
X
Figure 2: Exemplary graphical models for randomized controlled trials to infer the treatment effect (in light gray the observed variables). In classic Causal Inference (left), both the treatment T and outcome of interest Y are observed and unconfounded. In Prediction-Powent (center), Y is only measured indirectly via complex high sigh-dimensional measurements X, partially labeled. The missing Y are retrieved from X, training a predictive model on the annotated data. In Exploratory Causal Inference (right), the affected outcome Y unknown, still measured within X, from which model aims to identify it.
Causal Inference
Causal Inference. Causal Inference aims to quantify the effects of an intervention on a certain variable treatment some outcome variables of interest, Figure 2 (left). For simplicity, consider a binary treatment T = (0.1) 1) (e.g., taking a placebo or a drug) and outcome variables Y E (0, 1)" (e.g., binary indicators for symptoms, biomarkers, or clinical events). While contin- uous extensions would be interesting, we focus on discrete outcomes since continuous concepts in SAEs are well understood yet (Quirke et al., 2025). At population level we aim estimate the Average Treatment Effect (ATE):
(T = Y(T =
(1)
where Y(T = 1) and Y 0). or (1) and (()) for short, denote the potential outcomes under treatment and control Rubin 1974 (equivalently YT)o(T) 1 and Y|do(T) 0 according to Pearl (2009). Estimating T is challenging because, for each individual, only one potential outcome one under the received treatment- the counterfactual is missing (fundamental problem of causal inference (Holland) 1986)). This problem is mitigated in the sciences by performing, whenever possible, 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 IR of the outcome (no confounders), allowing (statistically) identify the ATE with the associational difference, i.e.,
factually observed-
= Y T = 1] - B|Y T = 0),
(2)
under standard causal assumptions (Rubin 1986 consistency (observing T 1, then Y Y()), and no interference across individuals (i.e., all individuals are independent samples from the popula- tion, and the treatment assignment to the individual does not affect individual j). It follows that the difference between the treated and control groups' sample means already unbiased estimator of the ATE. Nonetheless, more sophisticated estimators such as Augmented Inverse Propensity sophistrean
Weighting (AIPW (Robins et al. 1994) can achieve lower variance and thus greater efficiency.
Prediction-Powered Causal Inference and the rationalist approach. Assume that Y is latent and not observed directly. Instead, we observe indirectly within high-dimensional measurements C IRP, capturing all the affected outcome information, i.e., ( = O, mixed with the
E X other (latent) outcome causes W E R3, In our motivating example, let representing a well-defined behavior of interest and X its video recording, for which we don't 't have perfect behavior classifier yet. Prior work by Cadei al. 2024 2025) showed how to train a model on partially labeled data or similar experiments to predict factual outcomes Y & Y from X and then use them for causal inference. For simplicity, we assume that 7' is not directly observable in X, a common practice in double-blind randomized trials (e.g., neither the patient nor the doctor analyzing the results knows which treatment assigned). The set-up is illustrated in Figure ( (center). Both Causal Inference and Prediction-Poweredd Causal Inference represent rationalist approaches in scientific discovery, ignoring the hypothesis generation preliminary, i.e., data-driven Y definition.
3

---

Published as a conference paper at ICLR 2026
Exploratory Causal Inference and the empiricist approach. The rationalist approaches suffer the Matthew effect (Merton 1968), narrowing the effect hypotheses on the outcome of prior successful trials. In this paper, consider the setting where experiments model as the scientists having no or partial a priori knowledge of what the latent effect may be. This is shown in Figure 2 (right), with Y representing the unobserved and unknown latent factors affected by the treatment T and measure in X. 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 treatment effect in X (Rubenstein et al. 2017 Chalupka et al.) 2017). In other words, Y. W] the minimal and sufficient representation for X (Achille and Soatto 2018 Fumero et al. 2023 that renders the treatment independent from the observations, I.e., T
exploratory, which we informally
YJ. where only Y is causally affected by a controlled intervention on T. 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 that, when working with nigh-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 through a pretrained foundation model (FM) (Bommasani et al., 2022). obtaining representations h= (zx) Rdd whose geometry captures semantically meaningful regularities (Amir et al. 2022. Valeriani et al. (023). Throughout, we assume the FM is sufficient for the outcome information (Achille and Soatto, 2018), i.e., I(X, () I (x)),, Y). so working 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 is detectable 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 al.) 2023). We therefore reparameterize the representation into a sparse, interpretable measurement dictionary using sparse autoencoder (SAE) (Bricken al. 2023 Huben al. 2024]. Intuitively, the SAE ex- presses each h as 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 E IRd, the SAE computes a high-dimensional but sparse code E I&d and reconstructs linearly:
z s(h) g (E + be), h = D= bb,
(3)
where E, D E Ixdxm are respectively the encoder, and decoder linear maps, bes by E R are the learnable biases, and g : RT + R is the encoder nonlinearity (Bricken et al. 2023). Training minimizes a reconstruction loss with a sparsity penalty S weighted X 2 i.e.
min E[Ilh DE ball]] + x2()). D2200
Thereafter, each input can be summarized as h ~ ba + Ej Zjdj, where || < and D = [di,...,dm]] dm. This turns the FM representation into large dictionary of interpretable channels: each coordinate 2, 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 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 respond weakly to several distinct attributes, i.., weak polysemanticity and corresponding entanglement (Locatello et al. 2019). We need minimal language to talk about (i) the direction in code space associated
4

---

Published as a conference paper at ICLR 2026
with factor and (ii) how widely those directions spill across neurons. Let Z I be SAE codes and = .Y....., Y,) the (unknown) binary outcome factors with m > r. To define the leakage set and index, we first define the concept Y& neural representation
= B Z do = 1)] E Z do(Y; = 0) E I Ak E (1, (1.
(5)
and we say that the neuron 23 with j (1,..,,, m is activated by the factor Y& if [(vx)s] 2 & 0. When the neural effect representations {vkjk=1 are sparse and largely disjoint across coordinates, each effect factor "lights up" only few neurons, and different factors rely on different neurons.
Definition 3.1 (Leakage set and index). Fix a threshold & > O. In a ECI problem with effect neural representations {==)k=1 define the leakage set and leakage index, respectively,
A Ut: ((b))) 1=1
r
|Aee
Pe
m
If [A,]] > r, i..., PE > O, it indicates that many neurons respond to multiple factors, i.e,, polyse- manticity, whereas monosemanticity with respect to Y implies [A i.e., Pe 0.
Codes as statistical measurement channels. Under FM sufficiency and an (approximately) monosemantic SAF, 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 treatment-control mean shift using two-sample t-test, applying Bonferroni adjustment (Bonferroni] 1936) to control the family-wist error rate at regardless of the number of tests m. This provides an idealized measurement interface: we can scan Z for treat- ment-responsive channels and later interpret significant coordinates via the dictionary atoms d,.
Challenge: entangled effect representations. The above picture breaks down when leakage oc- curs, as any neuron entangled with the true affected outcome will eventually be identified as signif- icantly activated, while |Agl = (m)) >> r, challenging any interpretation. Intuitively, entangled neurons that primarily assigned to other concepts still activate differently depending Y. so with more powerful tests (larger sample sizes or stronger causal effects), they would be deemed sig- nificantly affected. Thereafter, classical multiplicity correction does not rescue interpretability here, leading to the paradox of Exploratory Causal Inference:
Paradox of Exploratory Causal Inference
In Exploratory Causal Inference, as the trial sample size the effect magnitude r grows, multiple testing, even with Bonferroni adjustment. redundantly returns all the outcome- entangled neurons as independent and significantly affected by the treatment.
We formalize these two phenomena below. Let Ty denote the treatment effect on code j.
Theorem 3.1 (Significance level collapse with sample size). Suppose at least pem neurons have nonzero effect [T,] 2 E > Via multiple testing, regardless of the Bonferroni adjustment,
Pr Pa[ j E As are rejected}
+
as 72 + 0o,
and the number of rejections converges to p.m in probability.
Proof sketch. For each j, the (-statistic is asymptotically normal with noncentrality A;- Vuty/o. The Bonferroni cutoff, which determines the significance of Tyz grows like /2 m; this cutoff is dominated by the growth in expectation of Tj (yn as - oc). Hence, any j with T, * 0 is eventually rejected. Without Bonferroni correction, the significance cutoff is constant. See full proof in Appendix
O
Theorem 3.2 (Significance collapse with effect magnitude). Fix < and let (3()) = =87 with > Via multiple testing, regardless of the Bonferroni adjustment,
Pr (all j E As are rejected?]
- as 0c,
5

---

Published as a conference paper at ICLR 2026
and the number of rejections converges to p.m in probabiliry.
vnsyg/o grows linearly in while the cutoff, even with Bonferroni correction, fixed for fixed m, n; every Y * eventually rejected. Details in Appendix
Proof sketch. The noncentrality ^y(s) =
Numerical illustration. Let T (ernoulli(0.5), Y T ((tt, 1) (single effect), and Z AZ 2B] mn where ZA Y (the effect principal channel) and ZB Y== ~ A(0001 1m-1, 1m-1) (entangled channels). As shown in Figure for 10 seeds, increasing ei- ther n leads the multiple testing to flag all the weakly entangled Z coordinates as signifi- cant, despite their negligible semantic relevance. This motivates the disentangling, stratified testing procedure introduced next (Section 4
Hejectoon
0.6
0.4
0.2
0.0
10
10
10.
Number samples (n)
Ellect size (K)
Bonferoni
FDR
I-test
Ground truth
Figure 3: The Paradox of Exploratory Causal Inference: Increasing the power of the test, the effect on any outcome-entangled code becomes significant, regardless its main interpretation.
4 NEURAL EFFECT SEARCH
To mitigate the multi-test significance collapse with entangled representation, i.c., Paradox Ex- ploratory Causal Inference, we propose NEuraLEFfecTSearCH (NES). novel causally princi- pled algorithm to disentangle the leaked effects by recursive stratification:
Algorithm 1 Neural Effect Search (NES)
1: function TEUURA.EFFECTSEARCE
2)
2: 77 < #{j: j E 5
number of hypotheses to test
3: for each neuron
do
4: (f,,P;) < NEURALEFEETTTTSTTTT Z,J,
D Pj tests Ho T, =
5:
end for
6:
R {j É s: < a/m ordered by [fyl (desc)
filter significant neurons
7:
i Ø then
8:
return S else
9:
10:
return NEURAALEFFECTSEARCHCCCZZ S, SUR))
end if
12:
end function
where NEURALEFFECTTEST (Algorithm 2 is the procedure for heltii-hypohhsiis testing on all the neurons j. by stratification (and potentially arm-wise residualization) over the already retrieved effects S. See Figure 4 for simplified illustration of NES procedure, Appendix B for NEURAL.FF FECTTEST description and Appendix
minimal Python implementation snippet. The key idea that we test all neurons simultancously, vanilla multiple testing cannot distinguish whether 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 multiple testing setting, in Line 6 we still perform Bonferroni correction by dividing the significance level a by m, preventing type error, i.e., false neural effects discoveries. In practice, if the sample size is

---

Published as a conference paper at ICLR 2026
very small, one make the test less conservative by relaxing the correction (which would return more, possibly false positives for the scientist to review).
a
4
&
(a) Estimate independently all the (b) Re-estimate the remaining neu- (c) Iterate until significant neu- neural effects (72,==22.72)) select ral effects controlling for the pre- ral effects measured, and vious discovery (Z1); select the turn all the selected neurons S strongest (T2,).
strongest (TZ,).
(Z, Zz}))
Figure 4: Illustrative example of the Neural Effect Search (NES) recursive procedure with two latent variables Y1, Y2 affected by the treatment and three measurement channels Z1, Zz. Zg, e.g., SAE codes, with Z1 principally aligned with Y1 and Z3 with Y2 (see principal alignment formal definition in Assumption A.2) At each iteration stratifying over the already selected neurons, c.g., Z1 after the first iteration, acts as a proxy controlling for the mediated effects by the corresponding (true) latent effects already identified, i.e., Y1.
Theorem 4.1 (Consistency of Neural Effect Search). Suppose the outcome neural represen- tation, i.e., SAE codes, captures and almost disentangles the treatment effects (still allowing for broad effect leakage). Then, as n + 00, the NES' output Sfmol satisfies
Pr Spmnl = Li,,. (ii,.....r))
1r)) -
where each ju a neuron coordinate principally aligned with a distinct affected outcome Yy-
Proof Sketch. At the first round, entanglement makes several coordinates look affected; neverthe- less, the coordinate most aligned with some true direction 2y maximizes the treatment effect and, under Bonferroni control, is selected with probability - as n + 2o. 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-zert (up to vanish- ing error). By repeating this argument, each iteration peels off one undiscovered principal direction until all r are recovered; thereafter no coordinate exhibits nonzero mean effect and the procedure halts. Hence Pr(Simal = {fI...., jrt) - 1 and Simil] + r. Further efficiency results, without loosing consistency, can be obtained with arm-wise effect residualization by the already selected neurons. See Appendix A for the complete formulation, proof and hypotheses discussion.
Discussion. NES recovers the r effect concepts in probability and terminates, sharp contrast with the paradox described earlier. While standard multi-hypothesis tests collapse with increasing power, i.e., and 5, 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, and bounding the collider bias, only the unidentified effect factor remains detectable. In this sense, NES does not merely test for effects: it disentangles the effects (under Assumptions A. A.3). identifying and adjusting the estimation of one true treatment effect factor at time until the entire effect subspace is recovered. Thus, NES can be interpreted both as multiple-testing correction method robust to entanglement and as a principled effect disentanglement algorithm.
7

---

Published as a conference paper at ICLR 2026
5 RELATED WORKS
Interpretable Heterogeneous Treatment Effect Estimation. A closely related line of work 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; [argagli- Stoffi et al. 2020) identify subpopulations with different responses, recognizing that pointwise es- timation 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 al., 2014) was introduced discover interventions in data rather than outcomes. In scientific trials, however, treatments are fixed by design, and the challenge 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 variillvs using equivalence classes of P(X do(T)). This requires density estimation in high high-dimensional spaces, which is generally infeasible. While clustering other metrics may be possible, CFL 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. (02T). Clos- est in spirit to our setting are interventional approaches (Varici et al. [023] 20244 Zhang et al. 2023] Yao al. 2025), which, even with all the necessary extra assumptions, would only offer identifica- tion results for the experimental settings W and not the outcome (í.e., the component invariant to the intervention (Yao et al.) p025 Therefore, they can not be applied 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 2023 Templeton et al. 2024 Huben al., 2024] Papadimitriou et al. 2025). Al- though SAES were imitially proposed as an interpretability tool (Bricken et al. (202)). a growing body of negative results, including spurious interpretability on random networks (Heap 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 mech- anisms rather than post-hoe 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 al., 2025) leverage SAES to surface human- understandable patterns correlated with target outcomes (e.g., engagement levels). which researchers can then treat 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, target causal effects and develop inference to assess which high- dimensional outcomes Y are affected, offering principled support for exploratory causal claims.
EXPERIMENTS
We validate our analyses (significance collapse paradox, and NES consistency) two complemen- tary settings: a semi-synthetic benchmark where ground-truth causal effects are known, and real- world randomized trial from experimental ecology.
6.1 SEMI-SYNTHETIC BENCHMARK
We simulated family of RCTs {T;, W,, Y.) 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 random image X; from the dataset per- fectly matching such attributes. Given the corresponding random sample X;
we (i) trained
SAE over the image representations encoded by SigLIP (Zhai 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 monose-
8

---

Published as a conference paper at ICLR 2026
manticity with respect the considered CelebA attributes (see Figure 8) 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 are reported in Appendix D and the main results (r = 2) are summarized in Figure Additional experiments testing (i) the required assumptions, (ii) method consistency with extensive ablations, and (iii) additional baselines are reported in Appendix B
Prosete
012-
0.5-
11:0-
100
011
300
3000
230
300
10003
131
2211
N
1.0
1.0
0.1
0.1 0.5
0.2
0.2
0.5
7op--2
Figure 5: Semi-synthetic benchmark. Precision, Recall, and IoU of different testing procedures across sample size (top) and effect size T (bottom). NES consistently achieves the best trade-off, avoiding the significance collapse of standard corrections.
Results. Increasing the power of the tests (increasing the sample size or effect magnitude T), all the methods eventually retrieve the true significant effects, i.e., Recall - 1. However, while all the baselines drop the Precision and corresponding IoU (Paradox of Exploratory Causal Inference), NES the only method that mitigates such entanglement biases. As expected, the Paradox doesn't emerge with very small sample (n 30) and effect regime (r 0.1), and more explorative ap- proaches, as vanilla t-test or top-k selection, could be preferred, at the price of potentially more false significant hypotheses, i.e., Precision << 1. With a yellow dot, 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 (cquivalent to the first step in NES), but then get confounded by the entanglement and miss the second one. While this is clearly 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-WORLDD RANDOMIZED TRIAL FROM EXPERIMENTAL ECOLOGY
ISTANT (Cadei et al. 2024) is an ecological experiment where ants from the same colony are randomly exposed to treatment or 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 then applied without Bonferroni adjustment due to the small sample size (n 44 videos) to discover seattment-sensitive codes, and only two neurons returned.
Results. Figure shows a qualitative interpretation of such neurons, by filtering the 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) seems to separate grooming events, already measured as significantly affected by the treatment in any previous rationalist approach to the exper- iment, i... 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 4 608 SAE's codes,

---

Published as a conference paper at ICLR 2026
Qualitation Inteppstation Neuron
groddee
Niciglt
Qualitaiive Interpetationn Seuron 550
Beiege Julgoen lolggrol
Balyrand backpoool
Figure 6: Exploratory Causal Inference for Experimental Ecology. Without any knowledge of the behaviors of interest, our procedure retrieves two significant treatment effects, interpreted as (i) grooming behavior and (ii) finite sample experimental design error, in full agreement with previous literature.
confirming the consistent results of our pipeline. The imperfect FI F1-score < 1 suggests the possi- bility of other entangled effects or broader representation, prohibiting linking the treatment effect on the interpreted outcome with the effect on such neuron without further labeling. The second neuron activated (code 550) represents a black position marking the background, i.e., a specific black color marking for dish palette positioning the videos recorded with such visible position marking (top left dish palette in the first batches of recordings) always assigned to the same treatment by chance due the small experiment size, as discussed the annotation bias by Cadei et al. (0224). Quantitatively, is exactly the most pre- dictive neuron for such characteristic (FI-score 0.568). The fact that the model also identifies the effect of the treatment assignment on the background due to the small sample size is strength of the method: it is still statistically significant signal and should not be ignored, even if interesting directly as biological effect. It is indeed the domain experts' duty to select which signal scientifically relevant or just useful to eventually (not necessarily) improve the experiment design.
the background (top right outline). Indeed, all
CONCLUSION
In this paper, 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 map one-to-one onto high-level concepts, and even weak 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 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 finite sample associations, e.g., background marking, that experts can readily dismiss. Overall, we view this work as a first step toward AI-driven efficiency gains 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, strongly assume that the observed variables X adequately capture information about the unknown Y, i.e. data sufficiency. For example, shrinkage in tumor is detectable via X-ray imaging, but. depending also reduce its metabolic activity, which is measured with PET scans. More complex measurement processes for X, e.g., multi-modal are natural extension of our work. Furthermore, we assume
the tumor type, treatment may
10

---

Published as a conference paper at ICLR 2026
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 imperfect, future iterations likely to improve. The good "identifiabilitt" assumption
our strongest. Promising early work already exists (Cui et al. 2025 Hindupur et al.) 2025 but
the identifiability theory of SAEs is not currently well understood as that of causal representa- tions (Yao et al.) (2025), c.g., still unclear how to deal with continuous concepts. In our paper, we took more empirical and future-looking stance 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 I 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 the Bellairs Research Institute, February 14/21, 2025, and particularly the discussions with Chandler Squires, Dhanya Sridhar, Jason Hartford, and Frederick Eberhardt and further feedback from Judea Pearl. Riccardo Cadei is supported by Google Research Scholar Award and a Google Google-initiated gift to Francesco Locatello. Tommaso Mencattini was supported by the ISTernship program. This research funded in part by the Austrian Science Fund (FWF) 10.5577//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 CC BY public copyright license to any author- acchor- manuscript version arising from this submission.
ETHICS STATEMENT
All datasets used this work are publicly available. In particular, the ISTAnt dataset (Cadei al., 2024) was annotated and pre-pn rre-processd by domain experts. Despite our method guarantees Identi- fication under untestable representation learning assumption (without supervision), any conclusion should not be interpreted as scientifically relevant without domain expert's 's interpretation. Ad- ditionally, 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 any- way necessary for inference, i.c., treatment effect estimation and uncertainty quantification.
REPRODUCIBILITY STATEMENT
All the datasets we use are publicly available and experiment details are thoroughly detailed in Ap- pendix E A snipped Python implementation for the main algorithm is also presented in Appendix

---

Published as a conference paper at ICLR 2026
REFERENCES
Alessandro Achille and Stefano Soatto. Emergence of invariance and disentanglement in deep rep- resentations. Journal of Machine Learning Research, 19(50):1-34, 2018.
Shir Amir, Yossi Gandelsman, Shai Bagon, and Tali Dekel. Deep vit features as dense visual de- scriptors, 2022. URL https:://///.. :ttps:///arka wttpiiiiiii///.i///aaa wttp://////.///...//22232 05814
Susan Athey and Guido Imbens. Recursive partitioning for heterogeneous causal effects. Proceed- ings of the National Academy of Sciences, 113(27):7333-736) 2016.
Susan Athey, Julie Tibshirani, and Stefan Wager. Generalized random forests. The Annals of Statis- tics, 2019.
Falco J Bargagli Stoffi,, Riccardo Cadei, Kwonsang Lee, and Francesca Dominici. Causal rule en- semble: Interpretable discovery and inference of heterogeneous treatment effects. arXiv preprint wwXiv:2009000030 2020.
Rishi Bommasani, Drew A. Hudson, Ehsan Adeli, Russ Altman, Simran Arora, Sydney von Arx, Michael Bernstein, Jeannette Bohg, Antoine Bosselut, Emma Brunskill, Erik Brynjolf- sson, Shyamal Buch, Dallas Card, Rodrigo Castellon, Niladri Chatterji, Annie Chen, Kathleen Creel, Jared Quincy Davis, Dora Demszky, Chris Donahue, Moussa Doumbouya, Esin Dur- mus, Stefano Ermon, John Etchemendy, Kawin Ethayarajh, Li Fei-Fei, Chelsea Finn. Trevor Gale, Lauren Gillespie, Karan Goel, Noah Goodman, Shelby Grossman, Neel Guha, Tatsunori Hashimoto, Peter Henderson, John Hewitt, Daniel E. Ho, Jenny Hong. Kyle Hsu, Jing Huang, Thomas Icard, Saahil Jain, Dan Jurafsky, Pratyusha Kalluri, Siddharth Karamcheti, Geoff Keel- ing, Fereshte Khani, Omar Khattab, Pang Wei Koh, Mark Krass, Ranjay Krishna, Rohith Ku- ditipudi, Ananya Kumar. Faisal Ladhak, Mina Lee, Tony Lee. Jure Leskovec, Isabelle Levent, Xiang Lisa Li. Xuechen Li, Tengyu Ma. Ali Malik, Christopher D. Manning, Suvir Mirchandani, Eric Mitchell, Zanele Munyikwa, Suraj Nair, Avanika Narayan, Deepak Narayanan, Ben New- man, Allen Nie, Juan Carlos Niebles, Hamed Nilforoshan, Julian Nyarko, Giray Ogut, Laurel Orr, Isabel Papadimitriou, Joon Sung Park, Chris Piech, Eva Portelance, Christopher Potts, Aditi Raghunathan, Rob Reich, Hongyu Ren, Frieda Rong. Yusuf Roohani, Camilo Ruiz, Jack Ryan, Christopher Ré, Dorsa Sadigh, Shiori Sagawa, Keshav Santhanam, Andy Shih, Krishnan Srini- vasan, Alex Tamkin, Rohan Taori, Armin W. Thomas, Florian Tramèr, Rose E. Wang, William Wang, Bohan Wu, Jiajun Wu, Yuhuai Wu, Sang Michael Xie, Michihiro Yasunaga, Jiaxuan You, Matci Zaharia, Michael Zhang, Tianyi Zhang, Xikun Zhang, Yuhui Zhang, Lucia Zheng, Kait- lyn Zhou, and Percy Liang. On the opportunities and risks of foundation models, 2022. URL wwtp://wwwwwg//bo//oooooo 200.://2008002722888
Carlo Bonferroni. Teoria statistica delle classi e calcolo delle probabilita. Pubblicazioni del R istituto superiore di scienze economiche e commericiali di firenze, 8:3-62, 1936.
Trenton Bricken, Adly Templeton, Joshua Batson, Brian Chen, Adam Jermyn, Tom Conerly, Nick Turner, Cem Anil, Carson Denison, Amanda Askell, Robert Lasenby, Yifan Wu, Shauna Kravec, Nicholas Schiefer, Tim Maxwell, Nicholas Joseph, Zac Hatfield-Dodds, Alex Tamkin, Karina Nguyen, Brayden McLean, Josiah E Burke, Tristan Hume, Shan Carter, Tom Henighan, and Christopher Olah. Towards monosemanticity: Decomposing language models with dictionary learning. Transformer Circuits Thread, 2023. URL.https. http://aaafoooooo.oo/ 0t002//mooosemmanic-cefeeoom -ereraanttci-ffttttteee www.ffatttussts. index. himl
çi rcu its.
Riccardo Cadei, Lukas Lindorfer, Sylvia Cremer, Cordelia Schmid, and Francesco Locatello. Smoke and mirrors in causal downstream tasks. arXiv preprint arXhv:2405.17151, 2024.
Riccardo Cadei, Ilker Demirel, Piersilvio De Bartolomeis, Lukas Lindorfer, Sylvia Cremer, Cordelia Schmid, and Francesco Locatello. Prediction-powerrt causal inferences. arXiv preprint arXiv:2502.06343. 2025.
Krzysztof Chalupka, Pictro Perona, and Frederick Eberhardt. Visual causal feature learning. arXiv preprint 11Xiv:1412.2309, 2014.
Krzysztof Chalupka, Frederick Eberhardt, and Pietro Perona. Causal feature learning: an overview. Behaviormetrika, 44(1)1177-16,, 2017.
12

---

Published as a conference paper at ICLR 2026
David Chanin, James Wilken-Smith, Tomáš Dulka, Hardik Bhatnagar, and Joseph Isaac Bloom. A is for absorption: Studying feature splitting and absorption in sparse autoencoders, 2025. URL net aotee//ooommmmmnCc/kk/////
Rayan Chikhi, Téo Lemane, Raphaël Loll- Lolp-Krippleber, Mercè Montoliu-Nerin Brice Raffestin, An- tonio Pedro Camargo, Carson J Miller, Mateus Bernabe Fiamenghi, Daniel Paiva Agustinho, Sina Majidian, et al. Logan: planetary-scale genome assembly surveys life's diversity. bioRxiv, pages 2024-07, 2024.
Sylvia Cremer, Sophie AO Armitage, and Paul Schmid- -emmil.. Social immunity. Current biology, 17(16):6933RR702 2007.
Jingyi Cui, Qi Zhang, Yifei Wang, and Yisen Wang. On the theoretical understanding of identifiable sparse autoencoders and beyond. arXiv preprint arXtv:2506.15961 2025.
Nelson Elhage. Tristan Hume, Catherine Olsson, Nicholas Schiefer, Tom Henighan, Shauna Kravec, Zac Satfield-Dodds. Robert Lasenby, Dawn Drain, Carol Chen, Roger Grosse, Sam McCandlish, Jared Kaplan, Dario Amodei, Martin Wattenberg, and Christopher Olah. Toy models of super- position. Transformer Circuits Thread,
2ub//022/aa toy_ /tt.eddee//ndx....m html
Kelly R Finn, Matthew J Silk, Mason A Porter, and Noa network analysis in animal behaviour. Animal behaviour, 149:7-22, 2019.
The use of multilayer
Marco Fumero, Florian Wenzel, Luca Zancato, Alessandro Achille, Emanuele Rodolå, Stefano Soatto, Bernhard Schölkopf, and Francesco Locatello. Leveraging sparse and shared feature activations for disentangled representation learning. Advances in Neural Information Processing Systems, 36:27622-27698,, 2023.
Thomas Heap. Tim Lawson, Lucy Famik, and Laurence Aitchison. Sparse autoencoders in- terpret randomly initialized transformers, 2025. URL fttpp:://arxiv.orrrabb//
17127
Sai Sumedh R Hindupur, Ekdeep Singh Lubana, Thomas Fel, and Demba Ba. Projecting as- sumptions: The duality between sparse autoencoders and concept geometry. arXiv preprint arXiv:2503.01822, 2025.
Paul W Holland. Statistics and causal inference. Journal of the American statistical Association, 81 (396):945-960, 1986.
Robert Huben, Hoagy Cunningham, Logan Riggs Smith, Aidan Ewart, and Lee Sharkey. Sparse autoencoders find highly interpretable features in language models. In The Twelfth International Conference Learning Representations, 2024. URL URLhttps: puattps://opeeee http://///////ee/eee//eomee wwt.:etttuooooeeeee
id=F76bwRSLeX
Patrick Leask, Bart Bussmann, Michael T Pearce, Joseph Isaac Bloom, Curt Tigges, Noura Al Moubayed, Lee Sharkey, and Neel Nanda. Sparse autoencoders do not find canonical units of analysis. In The Thirleenth International Conference Learning Representations, 2025. URL
https:://on /ttps///pppeeeiiieee net wwt.:/eeeeee.eeeeeeee
forum?ide Btte://ouumidddcaaelllll... Hea
Ziwei Liu, Ping Luo, Xiaogang Wang, and Xiaoou Tang. Large-scale celebfaces attributes (celeba) dataset. Retrieved August, 15(201 11, 2018.
Francesco Locatello, Stefan Bauer, Mario Lucic, Gunnar Rätsch, Sylvain Gelly, Bernhard Schölkopf, and Olivier Bachem. Challenging common assumptions in the unsupervised learn- ing of disentangled representations, 2019. /tRL:ttts::/aatt /ttp://///a/iva///aa http//axxiv..../a/aa/a wttp/rrg//abbaaa///r 12359
Wes McKinney et al. pandas: a foundational python library for data analysis and statistics. Python for high performance and scientific computing. 14(9):1-9, 2011.
Robert K Merton. The matthew effect in science: The reward and communication systems of science 1968.
considered. Science,
13

---

Published as a conference paper at ICLR 2026
Rajiv Movva, Kenny Peng, Nikhil Garg, Jon Kleinberg, and Emma Pierson. Sparse autoencoders for hypothesis generation. In Forty-second International Conference on Machine Learning. 2025. URL [R//ittps:///perrevieww Eor.ee/eooorumii1nn---
Maxime Oquab, Timothée Darcet, Théo Moutakanni, Huy Vo, Mare Szafraniec, Vasil Khalidov, Pierre Fernandez, Daniel Haziza, Francisco Massa, Alaaeldin El-Nouby, et al. Dinov2: Learning robust visual features without supervision. arXiv preprini urXiv:2304.07193, 2023.
Isabel Papadimitriou, Huangyuan Su, Thomas Fel, Sham Kakade, and Stephanie Gil. Interpreting the linear structure of vision-language model embedding spaces, 2025. URL https://arxxx.
org/ org/abs/ 2504 11695
Kiho Park, Yo Joong Choe, and Victor Veitch. The linear representation hypothesis and the geometry of large language models. arXiv preprint arXiv:2311.036553 2023.
Judea Pearl. Causality. Cambridge university press, 2009.
Kenny Peng, Rajiv Movva, Jon Kleinberg, Emma Pierson, and Nikhil Garg. Use sparse autoencoders to discover unknown concepts, not to act on known concepts, 2025. URL htttps/////s
org//bs/ 2506. 23845
Karl Popper. The logic of scientific discovery. Routledge, 2005.
Lucia Quirke, Stepan Shabalin, and Nora Belrose. Binary sparse coding for interpretability, 2025.
URL htt.thtsss//raiii..rrrggr.// abs/ 25596
James Robins, Andrea Rotnitzky, and Lue Ping Zhao. Estimation of regression coefficients when some regressors are not always observed. Journal of the American slutistical Association, 89 (427):846-866, 1994.
Rubenstein, S Weichwald, S Bongers, Mooij, D Janzing, M Groose-Wenttrn and Schölkopf. Causal consistency of structural equation models. In 33rd Conference on Uncertainty in Artificial Intelligence (UAI 2017), pages 808-811 8178817.4 2017.
Donald B Rubin. Estimating causal effects of treatments in randomized and nonrandomized studies. Journal of educational Psychology. 66(5):688, 1974.
Donald B Rubin. Comment: Which ifs have causal answers. Journal of the American statistical association, (1(6)))9661-99 9622, 1986.
Bernhard Schölkopf, Francesco Locatello, Stefan Bauer, Nan Rosemary Ke, Nal Kalchbrenner, Anirudh Goyal, and Yoshua Bengio. Toward causal representation learning. Proceedings of the IEEE, 10965)4612-634 2021.
Tore Schweder and Eil Spjøtvoll. Plots of p-values to evaluate many tests simultaneously. Biometrika, 69(3)-93-502, 1982.
Maciej Sypetkowski, Morteza Rezanejad, Saber Saberian, Oren Kraus, John Urbanik, James Tay- lor, Ben Mabey, Mason Victors, Jason Yosinski, Alborz Rezazadeh Sereshkeh, al. Rxxxl: A dataset for evaluating experimental batch correction methods. In Proceedings of the IEEE/CVF conference on computer vision and pattern recognition, pages 4285 4294, 2023.
Adly Templeton, Tom Conerly, Jonathan Marcus, Jack Lindsey, Trenton Bricken, Brian Chen, Adam Pearce, Craig Citro, Emmanuel Ameisen, Andy Jones, Hoagy Cunningham, Nicholas L Turner, Callum McDougall, Monte MacDiarmid, C. Daniel Freeman, Theodore R. Sumers, Edward Rees, Joshua Batson, Adam Jermyn, Shan Carter, Chris Olah, and Tom Henighan. Scaling monosemanticity: Extracting interpretable features from claude sonnet. Trans- circuits /204/2
former Circuits Thread, 2024. URL httpp:://trasstott/ee wwtp://eeaannntttttteeeieeeeeeee ieciiiitttyc http:iiiexxxxhee html
scaling hatgg-mmooeemattaaa
Lucrezia Valeriani, Diego Doimo, Francesca Cuturello, Alessandro Laio, Alessio Ansuini, and Al- berto Cazzaniga. The geometry of hidden representations large transformer models, 2023.
URL https: /tts:://axxiii org/ abs/ 2302. 00294
14

---

Published as a conference paper at ICLR 2026
Burak Varici, Emre Acarturk, Karthikeyan Shanmugam, Abhishek Kumar, and Ali Tajer. Score- based causal representation learning with interventions. arXiv preprint arXiv:2301.0822 2023.
Burak Varici, Emre Acartürk, Karthikeyan Shanmugam, and Ali Tajer. General identifiability and achievability for causal representation learning. In International Conference on Artificial Intelli- gence and Statistics, pages 2314-2322. PMLR, 2024.
Pauli Virtanen, Ralf Gommers, Travis E Oliphant, Matt Haberland, Tyler Reddy, David Couraaeau,, Evgeni Burovski, Pearu Peterson, Warren Weckesser, Jonathan Bright, et al. Scipy 1.0: funda- mental algorithms for scientific computing in python. Nature methods, 17(3):261-272, 2020.
John N Weinstein, Eric Collisson, Gordon B Mills, Kenna Shaw, Brad A Ozenberger, Kyle Ellrott, Ilya Shmulevich, Chris Sander, and Joshua M Stuart. The cancer genome atlas pan-cancer analysis project. Nature genetics, 45(10): 11100:11111-110000 2013.
Zhengxuan Wu, Aryaman Arora, Atticus Geiger, Zheng Wang, Jing Huang, Dan Jurafsky, Christo- pher D Manning, and Christopher Potts. Axbench: Steering LLMs? even simple baselines out- perform sparse autoencoders. In Forty- International Conference on Machine Learning, 2025.
net/ http://wwwwweeeeeooue.eeceec..ee wwwt/oorommadd/22222
jNyd
Dingling Yao, Dario Rancati, Riccardo Cadei, Marco Fumero, and Francesco Locatello. Unify- ing causal representation learning with the invariance principle. In International Conference on Learning Representations, 2025.
Xiaohua Zhai, Basil Mustafa, Alexander Kolesnikov, and Lucas Beyer. Sigmoid loss for language image pre-training. In Proceedings of the IEEE/CVF international conference on computer vision, pages 19955-11986, 2023.
Jiaqi Zhang, Kristjan Greenewald, Chandler Squires, Akash Srivastava, Karthikeyan Shanmugam, and Caroline Uhler. Identifiability guarantees for causal disentanglement from soft interventions. Advances in Neural Information Processing Systems, 36:50254-5000 2023.
15

---

Published as a conference paper at ICLR 2026
Appendix
SUMMARY
Proofs
17
Significance level collapse with sample size (Theorem 3.1)
17
A.2
Significance collapse with effect magnitude (Corollary 3.2)
17
A.3
Consistency Neural Effect Search (Theorem
18
B Neural Effect Test
23
Minimal Python Implementation Snippet
24
D Experiments Details
26
D.I CelebA semi-synthetic RCTS
26
D.2 ISTAnt
27
Additional Experiments
28
Assumptions Validation
28
E,2 Method Consistency
31
Additional Baselines
47
16

---

Published as a conference paper at ICLR 2026
A PROOFS
A.1 SIGNIFICANCE LEVEL COLLAPSE WITH SAMPLE SIZE (THEOREM 3.1
Theorem A.1 (Significance level collapse with sample size). Let Z E R be SAE codes and Tj the treatment effect on neuron j. By definition
[Ael= = P.m. As = {j |Ty 2
(7)
multiple testing at level a, regardless of Bonferroni correction
Pr(all j E Ag are rejected)
as n2 -> 20,
(8)
and the number of rejections Rn, satisfies
Rn + Pmm 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 ij be the estimated treatment effect and t, its t-statistic. Under stan- dard randomization, we have the asymptotic distribution
1 $ (A1), 1),
>,
vR Tj
(10)
where o² the asymptotic variance of 9z.
Multiple testing with Bonferroni adjustment rejects Hoj : if > 2a/(2m), where 2a/(2m) is the (1 - (2(2)) quantile of (0 1). As m - the threshold satisfies
(ra(22)))
2 logm. m.
(II)
For any j E Ag, we have * 0, hence Xy diverges at rate vn as n + co. Since vn grows faster than vlog m, follows that
Pr(Ity Za/(2m))
(12)
Therefore, for all j E Ae, the null is rejected with probability tending to one, and analogously
Pr(1k,1 > za/2) 1.
(13)
without Bonferroni adjustment. By the union bound,
Pr all j E Ag are rejected)
+ 1.
(14)
Hence, the number of rejections converges in probability to [Agl P.m. proving the claim.
A.2 SIGNIFICANCE COLLAPSE WITH EFFECT MAGNITUDE (COROLLARY 3.2
Corollary A.1 (Significance collapse with effect magnitude). Fix a finite sample size n., Sup- pose the treatment effects scale
(s(s) S j = L....,,m. m,
(15)
where s > is a scaling parameter and "ij are fixed coefficients. By definition
A = (i:
[Ael m.m. Pem.
(16)
In multiple testing at level a regardless of the Bonferroni correction,
Pr Pr(all all j E Ac are rejected) - as 0o,
(17)
and the number of rejections R, satisfies
Rg P.m. in probability.
(18)
17

---

Published as a conference paper at ICLR 2026
In words: even at a fixed sample size, amplifying the effect magnitude all the entangled neu- rons with the (true) affected outcomes are declared significantly affected by the treatment, regardless of being principally related other concepts.
Proof. For neuron j, the noncentrality parameter of the I-statistic under effect scaling 8 is
{5(5) = v (s)
yu 87j-
(19)
If 7/ 0, then (s)s) 0 for all and the rejection probability remains bounded by a/m.
If 7/ # O, then 2, + oo linearly in s, while the Bonferroni threshold (2/(2m) is fixed (since n, m are fixed). Therefore,
Pr(Ity] 2n/(2m))
as 8 30.
(20)
Analogously, without Bonferroni significance correction. Thus, for every j Ac, the null is eventually rejected with probability tending to one. By independence of limits,
Pr(all all Ar are rejected)
1,
(21)
and Rg - Pem in probability, completing the proof.
A.3 CONSISTENCY OF NEURAL EFFECT SEARCH (THEOREM 4.1
Given Randomized Controlled Trial, with randomized treatment T {0, 1). (unobserved) affected outcome Y E IR"", i.e., with non-null effect, and the SAE codes Z E Rm characterizing each individual/observation extracted from the indirect outcome measurements X X 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:
E[Y do(T=1)] - E.Y do(T=0)] E IR",
(22)
and the average treatment effect on the SAE codes:
7 = E 7
do - E[Z do[T= r
(23)
then,
77
Tk Uk VTY,
(24)
where the matrix V [V] 0r] E Rmxr aggregates in columns the r affected outcome neural representations (see Definition in 3). Assumption A.1 (Sufficiency). The matrix of code-level effect directions has full column rank, i.e, rVn =.
Discussion. By the neural treatment effect decomposition, i.e., Equation 24 every code-level con- trast lies in spanfut, (ut .., J, Assumption A.1 guarantees this span is truly r-dimensional (nonde- generate) and that the linear map rx + 7 is injective- distinct effect vectors YY produce distinct code-level contrasts. Informally, the mean-effect level, this behaves like "no loss of information" about yY when passing through V (akin to a sufficient statistic for yY a parametric family).
Assumption A.2 (Alignment). There exist distinct indices j1.....jr [m]] such that
[Kk.ja
max Ezk
We.5xl
Vk E [r].
(25)
each effect direction Up has a distinct principal neuron ja that strictly dominates the other effect directions by max. In addition, the following global Principal-Max property holds for the realized effect vector TY:
max JE[m
Utj
max kelrl
(26)
As special case, the following arguments also hold for binary affected outcomes and neuronal represen- tations in SAF.
18

---

Published as a conference paper at ICLR 2026
Discussion. Equation 25 supplies a distinct principal neuron (geometric dominance by max) per af- fected outcome factor. The global Principal-No -Mxx condition states that, in population, the overall argmax of the code-level contrast -² Vr is attained at some principal neuron. Because each NES round removes discovered effects from the sum, replacing Σi=1 in Equation 26 by a subsum the remaining (undiscovered) indices only reduces nonprincipal candidates; hence the argmax remains principal at every round.
Assumption A.3 (Arm-wise Effect Decomposition with e-Leakage). For any NES round & with discovered set 5 and any j S,
E Zs. do h2s) + Piat
LE (0,1),
(27)
where , is measurable w.r.f o [g) (o-algebra), and
Pj.1 Pi.
Σ
TV Vkgi
(28)
(x)((S)
with (() the affected outcome components already identified by S. Moreover, let G == g(Zs) be the pooled (Ireatment-agnosticc) stratification. Define the arm/stratun discrepancy
وو,( == E[Z G=g.T=#) E| G=g, do(T==)).
with vanishing transport error, after all affected outcome components are identified (i.e., when ((5)= = TT):
و 0 for all j & S, g. tE {0,
(29)
There exists constant
2 O such thut, for the weights wa used by the estimator,
Σ " ( Aso(o)) - se
for all j $
(30)
Finally, to ensure that principal coordinates remain identifiable in the presence of leakage, assume the (population) principal margin
= max
TR
max Jetnndd
Σ T Vtj
(31)
kE[r]
1=1
satisfies 2E.
Discussion. Assumption A.3 mean-level conditional requirement: conditioning within arms on the already-selected codes Zg explains their contribution in expectation, leaving only undiscovered effects in the adjusted contrast. In addition, Equation 30 is mild pooled-strutte transport bound: even though G is post-treatment and may induce collider opening, the weighted difference between observed and interventional arm means within strata is uniformly bounded by s and vanishes. In the linear (or locally linear) regime, the Jacobian of the mapping Y + Z satisfies òz/ōy = V (or more generally à E Z Y, do(Y = V), so the columns U/2 are Jacobian columns; Assumption A.2 requires principal dominance, while Assumption A.3 ensures additive mean structure and bounded transport error so that stratification cancels already- discovered parts up to uniform e bias.
Theorem. Under randomization, SUTVA, finite second moments with Lindeberg regularity, and Assumptions A. A.3 NES with pooled stratification on Zs and Bonferroni control selects direction per round and halts after rounds with probability 1, identifying all the principal components, i.e,
Pr Pr(Sinal= = (f1,..., +
E Sinal]
- r.
Note. Since the Theorem establishes Pr(Semal = ff.....jrll + 1, follows directly that also the overall family-wiss error rate (FWER) and false discovery rate (FDR) of the entire recursive NES procedure converge to 0.
We proceed by proving NES consistency, decomposing it in the following four steps:
19

---

Published as a conference paper at ICLR 2026
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 and, by As- sumption A.33 cancels the contribution of already-discovered directions up to 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 and is detected under standard CLT scaling,
4. by Assumption A.1 after r rounds no adjusted mean contrast remains beyond & and NES halts.
Step 1: Average neural treatment effect identification by randomization.
Proposition A.1 (Average Neural Treatment Effect Identification). For each coordinate j.
2
E Z
[T]] E[z do(T= = E|Z, T=
E|z T-0].
(32)
Proof. Randomization implies P(Z do(T=()) = P(Z T=t). Taking expectations and using SUTVA yields Equation 32
Step 2: Neural Effect estimation by pooled stratification: bounded bias and disentanglement.
At round é 1, Ø. there no stratification, and the corresponding associational difference identifies the average treatment effect by standard RCT results (shown in Proposition AA.1). At round > 1, build strata by deterministically binning Zg (pooled quantile cutpoints, ignoring T). For each stratum (T=t, L, G g). and fig their count.
G and arm é E {0, let j denote the sample mean of Zj among units with
For each j & s, define the post-stratified estimator
estrat
Σ
Wy (Z Zz,0u);
Wgg O B1g
+ Rlgg
(33)
SEg
see Algorithm for weight definition. Across & S, use Bonferroni level a/m and add the top- Sstrat rejection.
Lemma A.1 (Neural Effect estimation by pooled stratification: bounded bias and disentangle- ment). Let Patrat be defined by Equation 33 Then
pattrat
Pr((=-))B12)) G=g. do(T=))]]] -EE]) EiZ, G=g. do(T=0)) + B,, (34)
gES
where the leakage bias
By = 3y=>ugg Eug(e (مما(م)))) -
9EG
satisfies! |Byl S e by Equation 30
Under Assumption
A.3 the contribution explained by Zs
averages out within arm in the interventional means, giving
E
cstrat
Th Uk
S.
(35)
KEK(S)
Moreover, under finite second moments and Lindeberg regularity, the t-statistic of petrat is asymptotically normal with variance consistently estimated by the usual post-stratified Neyman
formula.
Proof. Add and subtract E|Z, G-g, do(T=()) inside each arm/stratum mean to obtain Equation
34 and identify By. Assumption A.3 yields Equation 27 and Equation 28 so averaging over G
cancels the hg.) part and preserves the stratum- inttum-invariant Pj.t. whose contrast equals Equation
28 combining with B,1 < gives Equation 35) The CLT follows from standard post-stratified difference-in-non inneness theory with finite second moments and nonvanishing stratum proportions. IT
20

---

Published as a conference paper at ICLR 2026
Step 3: NES one-step correctness.
Proposition A.2 (One-step correctness). Suppose the discovered set S retrieves exactly the principal neurons for the (S) affected outcome factors already identified. Then for any $ S.
E 7
[
Σ
Y T Vk.j
Se.
kEK(s)
By Assumption A.2 and the margin condition > 25 in Assumption A.3 the largest adjusted coordinate identifies, i.e., principal neuron, a new affected outcome and rejected, i.e. se- lected as significantly affected by the treatment, with probability - as - oc.
Proof. By Lemma A.1 the adjusted mean at j equals the over undiscovered directions up to Ee. Fix an undiscovered kt and its principal coordinate jk- given by Assumption The principal margin I > 28 ensures that the principal signal at jæ- dominates the maximal nonprincipal signal by more than 2e, hence remains strictly largest after the perturbation. Its f-statistic diverges at rate vn, so the maximizer over is a true undiscovered coordinate with probability 1.
Step 4: NES consistency by induction.
Theorem (NES Consistency). Under randomization, SUTVA, finite second moments with Lin- deberg regularity, and Assumptions A.3 NES with pooled stratification Zg and Bon- ferroni control selects one new direction per round and halts after r rounds with probability identifying all the principal neurons, ie.,
Pr(Sinal = .ri..)..i))) - 1,
E Stmal]
+
Proof. We distinguish between no affected outcomes, i..., r and at least one, i.c., r 2
If r (trivial), then TY and by Equation 24 also -2 Hence all adjusted expectations are O, coordinate is selected at any round, and Sftnal Ø with probability + 1 as n + 20.
I 2 with Tp * for each E ( (1....,r):
Base step. This is the special case of Proposition A.2 with the largest neural effect identifies principal direction and is rejected with probability - 1 as n + co.
Induction step. Suppose the beginning of round (1 l r) the discovered identifies exactly the e -1 distinct principal neurons identifying K(S). By Lemma A.1
[ostaat]
Σ
Uk.j
S
for every j & S,
(s)
i.e., the adjusted mean at any candidate coordinate depends only on undiscovered directions up uniform bias. Pick any undiscovered k=* & ((s)) and its principal coordinate ja- (Assumption | still applies to the remaining columns). By the margin condition I > 2s, the associated i-statistic diverges and the maximizer over is tied undiscovered direction with probability + 1.
Termination. Each round adds one previously undiscovered direction with probability
1. By Assumption A.1 (rank(V)) = r), there are exactly r linearly independent effect directions; after rounds they are all represented, and Lemma A.l together with the final- stage exactness equation 29 yields
Satrat =0
for every remaining j.
Hence, the corresponding t-statistics are (p() and, under Bonferroni control, no hypoth- esis is rejected with probability 1. Thus, no further selections occur, and Pr (Sánal (i,....j.)) - and [[[[a
21

---

Published as a conference paper at ICLR 2026
Comment. If pre-treatment effect modifier W influences the codes used to stratify (i.e., W + Zs)). pooled conditioning can create transport discrepancies; in that case, some additional SAE code outside S captures (part of) this modifier, the same margin argument ensures it will be selected, enlarge S, and-by Equation 2 discrepancy collapses thereafter. Conversely, if no such modifier projects into the stratification variables (i.e., W A Zs), then (g) = 0 already and no leakage arises.
Convergence Rate The proof of Theorem 4.1 shows that, each round and for each remaining principal neuron je. the corresponding (-statistic has noncentrality parameter of order vn. In par- ticular, the smallest principal margin that NES can detect with nontrivial power scales as O( 1/2), as in standard CLT-baaed tests.
Residualization (optional). The theory above uses pooled stratification on Zs with the e-leakage bound Equation 30 In practice, one may arm-wise residualize the tested coordinate Zj on Zs (c.g., by OLS within each arm) and then apply the same stratified contrast, or use plain arm difference. This targets the same estimand and can improve saitee power, but it is not strictly required.
Why it helps (variance reduction). Fix
and consider the (P T=t)) projection R,,-
Zj - B Zs with 3, arg ming [Z, B 2s) Tt)). Then
Var(R T-1) min Var(Z; - 3 Zs T-1) S Var(Z] T-1).
9
Thus, for any stratification weights, the usual Neyman variance for the difference in means built on Ry,, is weakly smaller asymptotically than that built on Zj (componentwise, within strata). Intu- itively, residualization orthogonalizes Zj against already-discovered codes within the arm, removing predictable variation and shrinking the standard error.
Why it can hurt (finite-sample and misspecification effects). If Be estimated (say 3.) 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 finite samples: although the population projection preserves the undiscovered mean contrast under Assumption A.3 an overfitted 3r can inadvertently subtract some of the undiscovered mean component (attenuating the signal and reducing power). Both effects vanish asymptotically if B, + Bt.
Validity and a safe recipe. If residualization is performed within amm and 3r is estimated on inde- pendent folds cample-spliting/crosstttiit fitting), then
Rg = E[R,, G- do-g)) + o(1),
and the Step 2 bounded-biassee bias/cancellation proof applies with Ry place of Zy. Hence, residualiza- tion is asymptotically valid and (typically) more efficient. In small samples without splitting, we still target the same estimand in expectation up to (1) under standard regularity, power can be non-monotone due to estimation noise.
Recommendation. We suggest using arm umm-wise residualization as a complementary efficiency device, with cross-fitting (or estimating 3, on previously discovered rounds) to avoid overfitting. It cannot worsen asymptotic validity, often improves power by reducing variance, and-inn and-implemented with splitting- reduce the practical impact of the bounded leakage in Equation 30
22

---

Published as a conference paper at ICLR 2026
B NEURAL EFFECT TEST
Algorithm Neural Effect Test (NET) with stratification on arm-wise residuals
1: function NEURALLFFECTTRRSCC. Z, J. S)
2: // A) Arm-wise residualize only the tested neuron j (optional)
3: if' = Ø then
4:
r, + Z.j (first round: no residualization)
5: else
6:
for t {0.1} do regress Z.j on Z, using only samples with T =
7:
for each with Ti rg Zej _( Z 9: end for
8:
end if
11:
B) Stratification from raw Ze
12:
if S Ø then
13:
put all units in single stratum: G {all}
(first round: no stratification)
14:
else
15:
compute pooled (ignore 7) medians/quantiles of each Z. 8 E S assign each unit to cell g(i) by binning Zi,s via those cutpoints
16:
17:
drop any stratum g with 181 = 0 or f0gg = 0
18:
end if
for each stratum g do Bigs Bog & treated/control counts in
20:
Pigs Hög f- treated/control means of ry in g
22:
ig 0g treated/control variances of ry in g
Bg + T&0g
23:
We + Σn (1ih + Tor
24:
end for
25:
7j
Σg W/g (Mig M0g
0ig
2
dūg
26:
V + Σg w
11g
nog
Tj
V2
27:
tt
V +
b Satterthwaite df
VV
(w? og / (w² 0dg/ (ggg/)))) max(n1g 1, max(nog 1,1)
Eger
+
28:
p 2 Pr([Te] 14)
tests Ho T
29:
return (f,, p)
30: end function
The algorithm tests whether neuron still carries residual causal contrast after accounting for already-discovered effects S. We first compute an arm-wise residual r, == Z; B(+) Zs. where ((3) 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 & by coarsening the raw Zg (e.g., medians/quantiles com- puted pooled over 7) and drop cells lacking both arms. Within each E G we take the treated-control mean difference of rj and aggregate with weights wy Big + nag- This is stan- dardization (g-computation):
7
Σ
Wy (T51g - T5.09)
E Σ (E() G. do( -Er, G, do(O)) -,,
9
23

---

Published as a conference paper at ICLR 2026
the estimator is unbiased under randommization/SUTTV.. The reported variance and watterthwaite df are the usual stratified formulas.
C MINIMAL PYTHON IMPLEMENTATION SNIPPET
We provide minimal Python snippet for our algorithm relying on pandas library (McKinney al. 2011) for tabular operations and SciPy library for statistical testing (Virtanen al. 2020)
Neural Effect Search
Recursive discovery.
def
NES (T, Z, S=[], alpha=0.05) 2.shape[1]
tests NET(T, (T, 2, S)
R tests. loc (tests "rasts["pe [""_value"] <= alpha/m) ]
if R.empty:
return
R. "ATE" L.bs () iixxmax
return NES (T, 8, S-S. apS.ap (j), a alphamalpha)
Neural effect Test By stratification with median binning. For simplicity, we ignore here arm- wise residualization (see full code for detailed implementation).
import pandas as pd import scipy
def NET (T, 2, S=111:
columns to test
cols = for in 2.columns if not in set (5)
if not cols: return ud.DattFramm (columns- ("neuron", "ATE", "p_value"])
build strata id dt () at dfl" "El"_T"] a.astype if S:
two groups per stratifier (median split); pooled (ignore T)
could use also df[s]>0 alternative
gid_bits (df[s)] df[s] .edian .astyp (int) for in of(" of["_gid"] co.con (gid bits, axis=1) apply (tuple, exis=1)
else:
dfl" df["_gid"] 0
len (df) out []
stratiff fy and test each neuron for in cols:
ATE 0.0
Vsum = 0,0
denom 0.0
for g. dg n_g len (dg) if n_g < 3:
df df..gropbyyy......ooo.oo...oo ("_gid")
continue
x1 dg. loc [dg 1" T"]
i]
x0 doc [dg 1 T"] 0, ]]
nl, n0 len (x1), len (x0)
if nl < 2 or n0 < 2: continue
24

---

Published as a conference paper at ICLR 2026
per-stratum summaries
mul, mu0 x1.mean (), x0.mean()
s1, s0 var (ddcf=1), vo. (ddof=1)
w n_ /
LOTP aggregation
ATE +-
(mul mu0)
V_g = (s1 n1) + (s0 n0)
Vsun += (#++2) =V_g
denom (=++ ((s1 / m])+* / max (nl 1) (s0 / n0)
(n0 1))
se VsumA*0.5 tstat ATE / se of (Vsum**2) denom pval 2.0 scipy. stw.s.t........... t...s.ffff.. (abs (tstat), df-df_wa _s)
out append ( float (ATE), float (pval)))
return pd. D...DaaFraaa (out, columns= ["ncuron", "ATE", "p_value"])
25

---

Published as a conference paper at ICLR 2026
D EXPERIMENTS DETAILS
D.1 CELEBA SEMI-SYNTHETIC RCTs
Dataset. We use CelebA (Liu et al. 2018), a face attributes dataset with 200k images and 40 binary attributes per image Furthermore, for implementation details, labels have been doubled (we pass from Beard to Has Bea and Has wwt.nntteeeee Beard.. 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-true truth binary labels. From this source, we simulate several RCTs fol- lowing the data-generating process (DGP) described below, varying the sample size (n < 200k) and treatment effect (r), 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 Bernoulli(0.5).
Outcome factors: we designate two binary effects Y=(Yi, Y2) using CelebA attributes: Y==yyelasssss, Yg=Wearing.Hatt
Exogenous Cause: W=Smi ling.
We implement "co-effect" model in which intervention 7 shifts both Y1 and Yg by the same ATE with arm-specific probabilities and W modifies only Y1, i.e,;
Pr(Y2=1 T= = (22)
Pr(Y==1 1 T- P6
(12)
P11 (t=1, w=
Pr(Yi=1 [[i=1|/=t,W-al W=w)=
Pio
(1)
(t=1, w=))
Po1 (1=0, w=1)
(1))
Poo (t=0, w=0)
with W (0rnoull((O.5). We vary effect magnitude via an ATE grid ATE E (0,0.1, (0,0.1,...,.0. (9
values). Concretely, starting from base rate 0.5, set:
Pi (22) 0.5 ATE
Po 0.5 ATE
(Y2)
and analogously for Y1 in the W= arm:
Pi1 (11) = 0.5 ATE
Pol (X1)
= 0.5
ATE 2
Pio
(1) = 0.2 + ATE Poo
(X1) = 0.2.
For each simulated unit, draw (T, W. Y1, Y2), then assign actual image whose CelebA at- tributes match the realized (Y1, Y2, W).
FM features. Each image is encoded with SigLIP (Zhii et al. 2023) into patch-level repre- sentation; we use the final-layer token features (dim 7-768, 196 patches/token positions averaged). 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 E I that serve hypotheses for treatment effect estimation. Thereafter, the details for the SAE in Table] [ Lastly, to turn hidden representation into hypotheses, aggregate patchwise by mean pooling to single Z E Ig 9216 per image. These per-image codes are the units we in NES and baseline procedures.
Evaluation. We evaluate discoveries against concept-aligned SAE codes extracted from CelebA. Let m= 216 the number of codes and (X) E IR the activation of code j E [m] on image X; a code is active when (x) > O. For true effect Y& E {0, 1} (here h E {1, and each code j.
we induce predictions 0/6 = (X,) > 0} and compute the Fl-score {0 in against the ground-truth labels {31 1= the best neuron for the concept is then
arg max F1 (1l JE(m]
1m p {um)
It can be downloaded from flwrlahs/celeha
26

---

Published as a conference paper at ICLR 2026
Component
Setting
Encoder nonlinearity
Top-k with k=5 active codes
Input dimension
768
Code / decoder dimension (m)
9216
Optimizer LR batch
Adam / 5xx001112 /20 20 1.0
Epochs grad clipping
Table 1: Training details for the SAE employed in semi-synthetic experimentss
The resulting ground-truth set of affected codes := {g1. 92] (in general [g] = r)). Each method (NES or baseline) returns set of discovered codes S S [m]. which we compare to & via set metries. Defining TP == |S g) FP = | g). and FN- G S), we report
TP
TP
F1 2 Precision Recall
Precision
Recall
TP + FP
TP FN
Precision + Recall
and the set Intersection-ovve--niin (loU)
Sgng U TP + FPNN
TP
IoU
For each trained representation, including the additional experiments in Appendix E. repeat the evaluation resampling the experiment times and reporting the average + standard deviation. Further ablations additionally retraining the encoder, i..., SAE, are presented in Appendix
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 posteriori for inter- pretationlevaluation 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 patch-level repre- sentation; we use the final-layer token features (dim d-384, 256 patches/token positions averaged). Unless noted otherwise, we do not use any task-specific fine-tuning.
SAE Details. We train SAE on the DINOv2 features to obtain interpretable codes Z E mh that serve as hypotheses for treatment effect estimation. Thereafter, the details for the SAE are in Table Lastly, to turn hidden representation into hypotheses, we aggregate patchwise by mean pooling to single Z IR 4608 per frame. These per-frame codes are the units we test in NES and baseline procedures.
Component
Setting (ISTAnt)
Encoder nonlinearity
top-k with 2= active codes
Input dimension
384
Code / decoder dimension (m)
4608
Optimizer LR/ batch
Adam 501000001110111 /
Epochs / grad clipping
10 1.0
Table 2: Training details for the SAE employed on ISTAnt.
Evaluation. Evaluation follows exactly the CELEBA protocol: we score discovered codes against ground-truth concepts via code-induced predictions and compute Precision/Recall/Fi and IoU for the set of returned codes (with domain annotations used only for interpreting and quantifying per- formance, not for training).
27

---

Published as a conference paper at ICLR 2026
E ADDITIONAL EXPERIMENTS
In this Section, we provide extensive empirical validation of our method, in addition to the selected main semi-synthetic experiments reported in Section 6 Particularly,
we explicitly test for the required encoder representation assumptions, theoretically justi- fying the successful identification results;
we extensively validate the method consistency by (i) repeating the experiments with dif- ferent encoders and trainings, (ii) comparing different method hyper-parameters, and (iii) additionally testing on more varied data-generating processes;
we additionally include two novel heuristic baselines, inspired by Causal Feature Learning principles (Chalupka et al. 2017).
Overall, the experiments consistently validate identification result and further provide practical guidelines on how to set the different hyperparameters.
E.1 ASSUMPTIONS VALIDATION
We assess how well SAE codes behave measurement channels CELEBA by testing the align- ment between individual neurons and the ground truth attributes described in the previous section. We consider the main SAE trained for the main experiments reported in Section 6 with training details described in Appendix [D and we then compare it with the same encoder replacing SigLIP (foundational model) with DINOv2, and again SAE top-k non linearity with Jump According to Theorem 4.1, we test if (i) such attributes information is still encoded in the SAE representation, i.e. Assumption A.I and (ii) per each attribute there exists dedicated neuron strongly aligned and all the other neurons are just marginally aligned with it, i.e., Assumption A.2 We first test the foundational model sufficiency and then for the SAF. Particularly, for each code j in the SAE representation, we treat the event Zj > 0 as a binary predictor and compute its F1-score against each attribute label (assumed given). We then interpret the most predictive neurons by visualizing their corresponding most activated samples; and visualize such attributes' entanglement in the rep- resentation by filtering all their most predictive codes and comparing their probing performances. We remark that in practice, without the affected outcome supervision, these assumptions are not testable, and we can do it here just because controlling the data- satta-enerating process and having ac- cess to attribute annotations. More indirect and unsupervised assessments for a SAE representation, testing a priori validity for NES, should be explored in future works, or just ignored, at the price of having no guarantees on the interpretability of NES results.
SigLIP with SAE top-k non linearity (main encoder). As expected, SigLIP embeddings are suf- ficient for the task, enabling us to accurately classify both the affected outcomes directly via (vanilla) logistic regression, respectively with Precision= 0.9639 and Recall= 0.9947 for Weari ng Hat, and with Precision= 0.9712 and Recall= 0.9747 for Eyeglasses Furthermore, in the SAE rep- resentation, trained with top-k non-linearity (k = 20), the two most predictive neurons for the two affected factors are: (i) neuron 38 for Wearing_Hts
with F1 score = 0.841, and (ii) neuron 6051 for Eyeglasses with F1 score = 0.748. We can further appreciate qualitatively the high separations by visualizing the most activated images per neuron in Figure 7 Also, the SAE represen- tation is then sufficient, and for each affected outcome, there is a principal neuron strongly aligned. In Figure & we visualize the Fi-score spectra of the most predictive neurons for each attribute. The long tail, dominated by principal component, represents exactly what is already required by As- sumptions AA.2 to enforce NES validity. Such low-amplitude but widespread correlations are precisely what triggers instead the Paradox of Exploratory Causal Inference with vanilla multiple- testing, i.e., with enough power all such entangled neurons are returned as significantly affected due to their (marginal) true affected outcome information. Our NES counters this issue by retriev- ing the leading effect first and then recursively stratifying on previously discovered codes, so that subsequent tests target the residual causal signal rather than previous causes' information leakages.
28

---

Published as a conference paper at ICLR 2026
Most activated images for Neuron 38
Most activated images for Neuron 6051
stronger activation (left panel) activation (left panel)
stronger activation (right panell activation (rightpanel)
Figure 7: Qualitative neurons' interpretations (SigLIP SAE top-k). Each panel shows the 12 most-activated test images for the most predictive neuron of each affected outcome concept (activation highest code value). Both concepts are perfectly separated.
Wicling Hot ncuron Importance
Eruplassos Insosance
neaooe
Nor 6353
0.4
4.2
nodiing cresg entrrgeeen
02
01
Figure 8: Assessing principal alignment with broad entanglement (SigLIP + SAE top-k). For each attribute, we rank SAE codes by Fl-score against the affected attributes and visualize the most predictive order. Both concepts are principally explained by a single neuron, and still weakly, while broadly entangled with many others.
DINOv2 with SAE top-k non-linearity As expected, also DINOv2 embeddings are sufficient for the task, enabling to accurately classify both the affected outcomes directly via (vanilla) logis- tic regression, respectively with Precision= 0.9534 and Recall= 0.9787 for Wearing Hat, and with Precision= 0.9636 and Recall= 0.9567 for Eyeglasses. Furthermore, in the SAE repre- sentation, trained with top-k non-linearity (k 20), the two most predictive neurons for the two affected factors are: (i) neuron 1 1937 for Wearing.Hoi Hat with F1 - score 0.431, and (ii) neu- 253 for Eyeglasses with Fl score 0.594. We further appreciate qualitatively the separations by visualizing the most activated images per neuron in Figure 9 Also, the SAE repre- sentation is then sufficient, while the principal alignment high for Eyeglasse ses but less evident for Hearing Hat, where the concepts could be possibly captured by all the top three most pre- dictive neurons. Indeed, also in the qualitative interpretation, among the most activated samples, some concepts, e.g., wearing sunglasses and hat, are over-represented. In Figure 10 we visualize the FI-score spectra the most predictive neurons for each attribute. The long tail, dominated by principal component, represents exactly what is already required by Assumptions A. A.2 enforce NES validity, even if the principal alignment is weakly satisfied by Wearing
tially violating Equation 26). Such low- www-ampitude but widespread correlations concept (poten- precisely what
trigger the Paradox of Exploratory Causal Inference with vanilla multiple-testim i.c., with enough power, all such entangled neurons returned as significantly affected due to their (marginal) true
29

---

Published as a conference paper at ICLR 2026
affected outcome information. Our NES counters this issue 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 previous causes' information leakages.
Most activated images for Neuron 1937
Most activated images for Neuron 253
stronger activation (left panel) weaker activation (left panel)
stronger activation (right panel) weaker activation (right parel)
Figure 9: Qualitative neurons' interpretations (DINOv2 SAE top-k). Each panel shows the 12 most-activated test images for the most predictive neuron of each affected outcome concept (activation = highest code value). Both concepts are perfectly separated, despite Wearing.Hat seeming to over-represent specific subgroups.
"Bearing hal neuror importatze
Eynglemms meamon importance
Ledddng Iodurt Teatus exargarent
00
Figure 10: Assessing principal alignment with broad entanglement (DINOv2 + SAE top-k). For each attribute, rank SAE codes by F1-score against the affected attributes and visualize the most predictive in order. Eyeglasses is principally explained by a single neuron, Bearing.tn Hat by three main neurons, and both concepts are still weakly but broadly entangled with many others.
SigLIP with SAE JumpReLU non-linearity We already discussed SigLIP embedding suffi- ciency in the main encoder hypotheses assessment. However, training on top SAE with jump- ReLU non-linearity breaks the desiderata hypotheses satisfied with top-k non-linearity. Particularly, the two most predictive neurons for the two affected factors are: (i) neuron 3485 for Wearing_Ha* with F1 - score = 0.273, and (ii) neuron 2865 for Eyeglasses with F1 - score = 0.425. Both performances are limited, particularly for Wearins Hat classification. We can further appreciate qualitatively the weak separability by visualizing the most activated images per neuron in Figure [] e.g., Neuron 3485 is not capturing precisely the concept Mearing.Hat but probably something broader like "having something on top of the head". e.g., some text from the background. In Fig- ure 10 we visualize the Fl-score spectra of the most predictive neurons for each attribute. For Eyeglasses, there exists principal neuron, despite the other entangled neurons still being suffi- ciently predictive. Instead, for Wear ing Hat classification, there is no clear principal component, violating NES assumption, and also ill-defining any evaluation attempts (requiring setting the princi-
30

---

Published as a conference paper at ICLR 2026
pal neurons identifying the effects). On such representation, NES has guarantees, and the long and heavy tails also trigger once again the Paradox of Exploratory Causal Inference with vanilla multiple-testing.
Most activated images for Neuron 3485
Most activated images for Neuron 2865
JANGO
vorve
B
MU
stronger activation (left panel) weaker activation (left panel)
stronger activation
weaker activation (right panel)
Figure 11: Qualitative neurons' interpretations (SigLIP + SAE jump-ReLU). Each panel shows the 12 most-activated test images for the most predictive neuron of each affected outcome cept (activation = highest code value). Eyeglasses is separated while is not the case for Wearing Hat Hat concept.
Weariing Hot neuror Impartarce
Eyoglazces neuron Importance
* Dest MLLEE 2013
636
028
rrddling tetveeeanngoee
822
8.0
Figure 12: Assessing principal alignment with broad entanglement (SigLIP SAE jump-ReLU). For each attribute, we rank SAE codes by F1-score against the affected attributes and visualize the most predictive in order. Eyeglasses concept is principally explained by single neuron, and still strongly and broadly entangled with many others. fearing.Hat concept has no principal components and the tails are very heavy, i.e., the information is shared among different neurons.
E.2 METHOD CONSISTENCY
In this Section, we extensively validate the method consistency beyond the experiments selected for the main results discussion in Section 6 Particularly, (i) we repeat the experiments with different encoders and trainings, (ii) we compare different method typer-parameters, and (iii) we additionally test more varied data-generating processes.
E.2.1 VARYING ENCODER
Considering the same data- tntta-genrratigg processes and evaluations described in Appendix D repeat the experiments relying on different measurement channels, i.e., input encoders and corresponding embedding.
31

---

Published as a conference paper at ICLR 2026
Foundational model First, replicate the main experiment replacing SigLIP with DINOv2 (Oqub et al., 2023) as foundational model. From the experiment in the previous paragraph, we know that the main hypotheses for NES to work hold, still triggering the Paradox of Causal Infer- ence if relying otherwise on vanilla multiple hypothesis testing. The results are reported in Figure As expected, DINOv2 perfectly replicates the results discussed in Section 6
13
0.8
0.8
0.8
Prockion
0.6
0.6
0.6
0.4
0.0
0.0
0.0
30
250
500
5000
30
250
500
5000
30
250
500
5000
N
1.0
1.0
1.0-
Prediston
0.4-
0.4
0.4
0.2
0.2
0.2
0.8
0.1
0.2
0.2
top-k
Figure 13: Ablation Foundationa Model (DINOv2). Precision, Recall, and IoU in effect identi- fication varying sample size N (top) and effect size r (bottom), relying on DINOv2 embeddings. NES consistently replicates the main results using SigLIP embeddings, still overcoming the paradox of Exploratory Causal Inference.
Sparse autoencoder dimension Then, we consider different sparse autoencoders varying the la- tent dimension m, and retrying with the same setting described in Appendix D Particularly, we varied m by factor [4, 6, 8, 10, 14, 16) of the foundational model dimension d 768 (in the main experiment, we considered m 12-d). In all the settings and retraining, replicate the results dis- cussed in Section 6 i.c., NES consistently overcomes the Paradox Exploratory Causal Inference, while consistently invalidates all the other baselines, making both method and the baselines invariant with respect to the latent representation dimension, in the order a few thousand neurons. See results summaries in Figures 14
32

---

Published as a conference paper at ICLR 2026
1.0-
Predaion
0.6
0.4
0.4
0.4
0.2
250
500
5000
30
250
5000
250
500
5000
1.0
0.8
0.0
0.8
Practsion
0.2
0.2
0.2
7
0.0
0.0
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.8
NES
Bonferroni
FDR
t-test
top-k
Figure 14: Ablation SAE dimension (m = 3 072). Precision, Recall, and IoU in effect identifica- tion varying sample size N (top) and effect size 7 (bottom), with SAE dimension
072, 4x DINOv2 dimension = 768. NES consistently replicates the main results, varying the representa- tion dimension m, still overcoming the paradox of Exploratory Causal Inference.
1.0
1.0
1.0-
0.8
0.8
0.8
Practsion
0.2
0.2
0.2-
0.0
0.0
0.0
30
250
500
5000
30
250
500
5000
30
250
500
5000
N
Proctaion
0.8
0.6
0.6
0.0
0.0
NES
Bonferroni
FDR
E-test
top-k
Figure 15: Ablation SAE dimension (m 608). Precision, Recall, and loU in effect identifica- 4 608, 6x DINOv2 dimension n = 768. NES consistently replicates the main results, varying the representa- tion dimension m, still overcoming the paradox of Exploratory Causal Inference.
tion varying sample size N (top) and effect size 7 (bottom), with SAE dimension
33

---

Published as a conference paper at ICLR 2026
1.0-
Predaion
0.4
0.4
0.4
250
500
5000
30
250
5000
250
500
5000
1.0
0.8
0.0
0.8
Pradtsion
0.2
0.2
0.2
0.0
0.0
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.8
NES
Bonferroni
FDR
t-test
top-k
Figure 16: Ablation SAE dimension (m = 6 144). Precision, Recall, and IoU in effect identifica- tion varying sample size N (top) and effect size 7 (bottom), with SAE dimension DINOv2 dimension n = 768. NES consistently replicates the main results, varying the representa- tion dimension m, still overcoming the paradox of Exploratory Causal Inference.
144, 8x
1.0
1.0
1.0-
0.8
0.8
0.8
Practsio
0.6
0.2
0.2
0.2-
0.0
0.0
0.0
30
250
500
5000
30
250
500
5000
30
250
500
5000
N
Proctaion
0.8
0.6
0.6
0.0
0.0
NES
Bonferroni
FDR
E-test
top-k
Figure 17: Ablation SAE dimension (m 680). Precision, Recall, and loU in effect identifica- tion varying sample size N (top) and effect size (bottom), with SAE dimension 7 680, 10x DINOv2 dimension n = 768. NES consistently replicates the main results, varying the representa- tion dimension m, still overcoming the paradox of Exploratory Causal Inference.
34

---

Published as a conference paper at ICLR 2026
1.0
Predaion
0.6
0.4
0.4
0.4
250
500
5000
30
250
5000
250
500
5000
0.8
0.0
0.8
Practsion
0.2
0.2
0.2
0.0
0.0
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.8
NES
Bonferroni
FDR
t-test
top-k
Figure 18: Ablation SAE dimension (m 10 752). Precision, Recall, and IoU in effect identifica- tion varying sample size N (top) and effect size (bottom), with SAE dimension 10 752, 14x DINOv2 dimension = 768. NES consistently replicates the main results, varying the representa- tion dimension m, still overcoming the paradox of Exploratory Causal Inference.
0.8
0.8
0.8
Procision
0.6
0.6
0.6
0.4
0.0
250
5000
0.0
30
250
5000
0.0
30
250
500
5000
N
1.0-
Predision
0.6
0.4
0.4
0.4
45
0.8
0.1
0.2
top-k
Figure 19: Ablation SAE dimension (m 12 288). Precision, Recall, and IoU in effect identifica- tion varying sample size N (top) and effect size (bottom), with SAE dimension m = 12 288, 16x DINOv2 dimension n 768. NES consistently replicates the main results, varying the representa- tion dimension m, still overcoming the paradox of Exploratory Causal Inference.
Sparse autoencoder non-linearity Additionally, consider different sparse auto-encoder non- linearities and repeat all the experiments as before. In Figures 20[23] we report all the results using top-k activation with & (5, 10, 50, 100) (by default 20 in the main experiments). Again,
35

---

Published as a conference paper at ICLR 2026
all the results discussed in Section 6 are replicated, ie., NES consistently overcomes the Paradox of Exploratory Causal Inference, suggesting the top-k selection is not influential for our method, Le., the required assumptions significantly change. On the other hand, the other baselines consistently fail due to the Paradox of Exploratory Causal Inference, and the higher the enforced entanglement, i.e., k, the higher the broad entanglement with the affected outcomes, and accordingly smaller the precision. Finally, any analysis using jump-ReLU for non-linearity invalid due to the principal alignment discussed above, required both for NES validity and more generally for valid evaluation. For completeness, we report anyway in Figure 24 the replicated experiments results using jump- ReLU non- non-linearity. At least one, if not both, ground truths are ill-defined, and the consistent null precision, even for NES, should be taken with pinch of salt.
consistently satisfied, despite the obtained representation may
1.0
1.0
1.0-
0.8
0.8
0.8
Proctsion
0.6
0.2
0.2
0.2-
0.0
0.0
0.0
30
250
500
5000
30
250
500
5000
30
250
500
5000
N
Proctaion
0.8
0.6
0.6
0.0
0.0
NES
Bonferroni
FDR
E-test
top-k
Figure 20: Ablation SAE non-linearity (top-5). Precision, Recall, and IoU in effect identification varying sample size N (top) and effect size (bottom), with SAE non-linearity by top-k with & = 5. NES consistently replicates the main results using top-k with 20, still overcoming the paradox of Exploratory Causal Inference.
36

---

Published as a conference paper at ICLR 2026
1.0-
Predaion
0.6
0.4
0.4
0.4
0.2
250
5000
30
250
5000
250
500
5000
1.0
0.8
0.0
0.8
Pradision
0.2
0.2
0.2
0.0
0.0
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.8
NES
Bonferroni
FDR
t-test
top-k
Figure 21: Ablation SAE non-linearity (top-10), Precision, Recall, and IoU in effect identification varying sample size (top) and effect size (bottom), with SAE non-linearity by top-k with k 10. NES consistently replicates the main results using top-k with k 20, still overcoming the paradox of Exploratory Causal Inference.
1.0
1.0
1.0-
0.8
0.8
0.8
Practsion
0.2
0.2
0.2-
0.0
0.0
0.0
30
250
500
5000
30
250
500
5000
30
250
500
5000
N
Proctaion
0.8
0.6
0.6
0.0
0.0
7
NES
Bonferroni
FDR
E-test
top-k
Figure 22: Ablation SAE non-linearity (top-50). Precision, Recall, and IoU in effect identification varying sample size N (top) and effect size (bottom), with SAE non-line non-lincarity by top-k with k 50. NES consistently replicates the main results using top-k with = 20, still overcoming the paradox of Exploratory Causal Inference.
37

---

Published as a conference paper at ICLR 2026
1.0-
Predaion
0.4
0.4
0.4
0.2
0.2
1
250
500
5000
30
250
5000
250
500
5000
1.0
0.8
0.0
0.8
Practaion
0.2
0.2
0.2
11
0.0
0.0
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.8
NES
Bonferroni
FDR
t-test
top-k
Figure 23: Ablation SAE non-linearity (top-100). Precision, Recall, and IoU in effect identification varying sample size (top) and effect size (bottom), with SAE non-linearity by top-k with & 100. NES consistently replicates the main results using top-k with h 20, still overcoming the paradox of Exploratory Causal Inference.
1.0
1.0
1.0
0.8
0.8
Pruolsion
0.4
0.2
0.2
0.2
0.0
250
500
5000
30
250
500
5000
30
250
500
5000
N
0.8
0.8
0.8
Procision
0.6
0.6
0.6
0.4
0.0
0.0
0.0
0.8
0.1
0.2
0.5
NES
Bonferroni
FDR
E-test
top-k
Figure 24: Ablation SAE non-linearity Reun--ReLU). Precision, Recall, and IoU in effect identi- fication varying sample size N (top) and effeet size 5 (bottom), with SAE non-linearity by jump- ReLU. The principal alignment is violated, invalidating both NES and any evaluation (ill-defined ground truth).
Seed Finally, we replicate two more times exactly the same main experiments presented in Section 6). retraining the SAE with different random seed. Once again, replicate the results discussed
38

---

Published as a conference paper at ICLR 2026
in Section 6 i.e., NES consistently overcomes the Paradox of Exploratory Causal Inference, while it invalidates all the other baselines. See results in Figures 25 26
Prediton
0.6
0.6
0.6
0.4-
0.4
0.4
15
30
250
250
1.0
1.0
1.0-
0.8
0.8
0.8
Pricisin
0.6
0.2
0.2
0.2-
0.0
0.0
0.0
0.1
0.2
0.3
0.0
0.1
0.2
0.5
0.0
0.1
0.2
0.5
0.8
NES
Bonferronl
FDR
t-test
top
Figure 25: Replica-1 main results. Precision, Recall, and IoU in effect identification varying sam- ple size (top) and effect size (bottom), retraining the SAE with a different random seed (replica 1). NES consistently replicates the main results, still overcoming the paradox of Exploratory Causal Inference.
1.0
1.0
1.0-
0.8
0.8
0.8-
Practsion
0.2
0.2
0.2-
0.0
0.0
0.0
30
250
500
5000
30
250
500
5000
30
250
500
5000
N
Proctaion
0.8
0.6
0.6
0.0
0.0
NES
Bonferroni
FDR
E-test
top-k
Figure 26: Replica-2 main results. Precision, Recall, and loU effect identification varying sam- plc size N (top) and effect size (bottom), retraining the SAE with different random seed (replica 2). NES consistently replicates the main results, still overcoming the paradox Exploratory Causal Inference.
39

---

Published as a conference paper at ICLR 2026
E.2.2 VARYING METHOD HYPER-PARAMENE PARAMETERS
We now repeat the main experiments and compare different variants of our methods, varying the muliiple-hpothheii testing, using residualization and varying the ATE estimator.
Hypothesis Testing We compare three per-round gates inside NES: Bonferroni, FDR, and f-test. Same setup as described in Appendix [D] with extended sample size N and effect size grids, as considered in the additional experiments described in Appendix E.2.3 only the multiplicity rule changes while recursion and residual stratification are unchanged. The results are reported in Figure
27 Bonferroni adjustment and FDR deliver the best recoveries, full recall, keeping Precision with sufficient experiment power. NES-t is comparable overall, with similar performances with higher power, potentially more exploratory for very small power, i.e., N 30, and less precise in mid-power regimes, i.e., N E (50....,500) 5000. т E (0.2, 0.6) (weak Paradox of Exploratory Causal Inference). The results suggest generally preferring i.e., Bonferroni and FDR, when the power of the experiment is sufficiently high, while considering the 1-test for more explorative approach in very low power regime.
multi-hypothesis testing correction,
1.0m
10-
14-
0.5
10003
0.2
02-
0.2
0.0
0.0
0.8
00
250
100
1000
2500
0000
53
50
100
200
100
1000
2500
5000
30
100
200
500
1000
2500
5000
1.00
1.0
1.0
0.5
08-
0.8
0.2
02-
0.2
0.0
0.0
0.0
0.1
0.
Bedence
EDR
Figure 27: Ablation multi-hypotheses testing (within NES). Bonferroni and FDR: best recoveries, full recall, keeping Precision Z 0 with sufficient experiment power; l-test: comparable overall, with similar performances with higher power, potentially more exploratory for very small power, and less precise in mid-power regimes.
Residualization We then evaluate the benefits in combining the recursive stratification procedure characterizing NES, with or without arm-wise residualization within NeuralEffect Test (lines 2-10) for each multi-hypotheses testing method. Same experiment set-up as described in Appendix D Results are reported in Figure 28 In lower power experiments, i.e., smaller n or T, arm-wise residualization seems to consistently improve the precision without compromising the recall, for each multi- multti-hypothesss testing variant. higher power experiments, i.e., greater n or 7, such differ- gets negligible as discussed in Theorem 4.1 discussion in Appendix A
40

---

Published as a conference paper at ICLR 2026
0.4
165
80
0.0
100
N
N
3.44
1.0
1.0
0.54
62-
65
Dualaroa NSS
7D0 XC1
Fran NES
Figure 28: Ablation arm-wise residualization (within NET), Additional arm-wise residualization significantly improve the method performances in lower power regime, i.e., smaller sample duced effect.
Average Treatment Effect estimator Throughout the paper, our per-neuron hypothesis test uses the associational difference (AD), i.e., two-sample t-test the treated-conie difference in means. In randomized trials, AD is unbiased for the ATE, but is not cemi-paramettically effi- rrriance-reduction cient. A standard variance- reduction alternative Augmented Inverse Propensity Weighting (AIPW;
Robins et al., 1994), which orthogonalizes the estimator against misspecification of either the propensity score the outcome regression. For each code j. let Zij be its activation for unit T: E {0, }} the treatment, and W; observed exogenous causes. We compute the AIPW pseudo- outcome
T. Zi, = (W;(W;) - (aoo(W + (WW) 1
1- 1 1 TWW)) (Ziz (oo(WW)),, (36)
where T +WW) = Pr(T (W) EiZ, T t, W] is muisance regression. The AIPW estimate of the code-level ATE AAIP
W), known and constant π = 0.5 balanced RCTs, and
1 E. Zey: test Ho T, 0 via one-sample t-test on {Zn}] with robust variance. Figure 29 reports the standalone multiple testing methods performances comparing AD vs. AIPW neural treatment effect estimator, fixing the effect magnitude ple sizes n E {30, 500, 5 000}. In our setting, with balanced and randomized treatment assignment (α = 0.5) and a single binary effect-modifier W. AIPW yields only marginal efficiency gains: Pre- cision/Recall/ooU curves are essentially overlapping, with small stability improvements for AIPW the smallest n. Crucially, orthogonalization affects variance but does not resolve entanglement: the significance-collassc phenomenon for standard multi-testing (Section 3 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 estimated. Takeaways:
0.6 and across sam-
in pure RCTs with weak, low-dimensional W, AD is competitive and simpler,
AIPW 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,
regardless of AD or AIPW, NES's stratified recursion is the key to avoiding over-discovery under entanglement.
41

---

Published as a conference paper at ICLR 2026
Bonferroni
5-test
top-k
1.0
0.8
0.0
0.4
0.2
0110
Pantaiio
Recall
Precaion
Precaion
Recall
Procaion
0.2
0.0
Predekon
Hooall
Precsion
Heeall
Predakn
Rooall
Presskon
Heeall
1.0
0.8
Precaion
Recall
Precaion
Recall
Fression
Rocall
Precaion
Recall
Figure 29: Ablation Treatment Effect Estimator. Precision, Recall, and IoU when replacing the per-neuron causal estimator AD (associational difference) with AIPW for vanilla multiple testing criteria (baseline).
E.2.3 VARYING STRUCTURAL CAUSAL MODEL
Additional main results reporting all the considered sample sizes and effect magnitudes in the sera-eeeeeatingg processes, for two evaluation regimes:
This paragraph expands the quantitative results illustrated in Figure 5 by
1. Unknown number of effects (r). Each method returns its own set of significant codes. We then report Precision, Recall, and IoU against the ground-trun truth affected codes.
Known number of effects (r). We assume to know the true number of effects, and we just look at the highest effects for each method. We again compute Precision, Recall, and IoU (namely, apply top-2 selection on top of other methods).
As detailed in Appendix D.I we vary (i) the sample size n E {30, 50, 100, 250, 500, 1000) and (ii) the ATE magnitude 7 E [0.1, 0.2. 0.8). holding the semi-synthetic DGP and SAE training protocol fixed. Across both regimes and over the entire grid, NES maintains high Precision and loU while matching the best Recall of baselines. When the experiment power increases (larger or r), vanilla t-tests and classical multiplicity corrections (FDR/Bonferroni) exhibit the sig- mificance-collapee behavior: Recall saturates but Precision drops sharply as leakage neurons be- come significant, driving loU toward zero. Enforcing the correct cardinality (r known) mitigates sele-telection but does not resolve entanglement: baselines still replace a true effect with a leak- age 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.
42

---

Published as a conference paper at ICLR 2026
1.0
1.0-
1.-
0..
0.8
0.8
0.6
Rocall
0.6
0.6
0.4
0.4
0.2
Bonfereoni I-teet top-k
Bonferronn E-test top-
NES BonnferonnnD A-teet top-
Methods (bars shuded by N)
Mothods (bars shaded by N).
Methods tham shaded by N)
Shandes N
1.0
0.8
0.8
0.5
Prottde
0.6
0.6
0.6
0.4
0.4
0.1
0.2
0.2
0.2
0.00
NES BonferrmiFDD
top Methods (loars slnded by
NESBoufervoFFDD top
NES DouferronPDD
top
Metthodk (lott sluded by x)
Methood (bars shouled by 1)
Sharles by
Figure 30: Full results with r unknown. Precision, Recall, and IoU for all methods when each returns its own set of significant codes level a= 0.05.
43

---

Published as a conference paper at ICLR 2026
1.0
1.0-
1.0
01.
0.8
0.5
0.6
Rocall
0.6
0.6
0.4
0.2
NES Bonferronil DDR I-teet top-k
Bonferroni (-test top- Mothods (bars shaded by N)
NES (ennferronrn A-teet tope Methodo tham shaded by N)
Methods (bars shuded by N)
Shandes
1.0
0.8
0.8
0.5
Prottée
0.6
0.6
0.6
0.4
0.4
0.1
0.2
0.2
0.2
0.00
NES DonferrmnFDD top
NESBoufervaFFDD top
NES BouferoooDDD
top
Methouls (loars slanded by 7)
Mettlode (lott sluded by x)
Methodds (bars shouled by 1)
Sharles by
Figure 31: Full results with r known (top-r selection). Precision, Recall, and IoU when every method is forced return the codes (true number of effects) with the highest absolute treatment effect.
No effect We repeat the experiments described in Appendix D removing both the effects, namely imposing T = In this setting. a valid discovery procedure should return no significant neurons.
Figure 32: Zero-effect ablation. Number of significant neurons retrieved by method when effects present, i.c., optimal if not retrieving anything.
We keep the matta-gnnraatig process, foundation model, SAE training, and testing grid over sample sizes n as described in Appendix[D] changing only the interventional contrast to ATF 0. For each method, we record the number of discoveries per run. Across all sample sizes, NES consistently returns an empty set: in the first iteration, no neuron survives Bonferroni at level a/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 l indices by design, labeling pure noise significant. This behavior matches our theoretical intuition: with = there is no effect vector to leak into entangled coordinates, so the paradox discussed in Section does not arise; still procedures that control multiplicity (NES via its first-step
44

---

Published as a conference paper at ICLR 2026
Bonferroni gate, Bonferroni, and FDR) appropriately abstain, whereas selection rules that ignore multiplicity (top-k, vanilla t-tests) over-discover, collapsing the method precision.
Opposite effects To stress-test effect identification under more complex causal structure, we ex- tend the main RCT simulation by allowing the two outcome components Y1 and Yg to have differ- ent treatment effects (even complementary). As before, each synthetic unit corresponds CelebA image whose attributes match the realized (Y1. Y2. W) triple. We fix T ~ Bernoull((O.5) and W (ernoulli(O.5). and we retain the co-effect model described in Appendix D but now vary the two ATES over grid of ordered pairs (TI, 72) E {0.22 0.8), (0.3, 0.7), (0.8, 0.2) thus controlling the gap between the two causal effects. For each pair, we set the treatment- shift for Y2
real
(12) Pi
0.5 + 3
(12) Po
0.5 3.
(37)
while Y1 additionally depends W:
(1) 0.5 3.
(t=1,==1)
Pio (V)) 0.2 T1
(t=1, w=0),
1 ww)
(38)
(8)) = 0.5
PoI
(t=0, w=1),
P0o = 0.2,
(X.)
(t=0, w=
This yields a controlled spectrum of settings in which Yi and Y2 express treatment effects of varying and potentially opposite magnitudes. For each (T1, T2) and sample size N E (500, 5000), we draw (T, W, Y1, Y2). attach the matching real image, and apply NES and baselines to evaluate precision, recall, and IoU across the full two-effect grid. The results are reported in Figure 33 34 and consis- tently replicate the evidence discussed in the main experiments, i.e., NES overcoming the Paradox of Exploratory Causal Inference, opposed any other baselines. As expected. with enough periment power, c.g., couple, while with lower power, e.g., N 500, both NES and some vanilla bascline can struggle in retrieving all the the effects (perfect recall) one or both the signals are very limited (as for the main experiments).
000, all the methods consistently return the same results for any effects
0---
0.64
0.2
0.0
Figure 33: Ablation opposite effects (N 500). Precision, Recall, and IoU in effect identification varying the two effects difference in the main structural causal model (fixing N = 500), NES con- sistently replicates the main results, still overcoming the paradox of Exploratory Causal Inference.
45

---

Published as a conference paper at ICLR 2026
100
Prodern
0.4
62
63
011
0.
0.0
0.5
0.1
0.6
06
44
48
30
30
66
0.5
0.5
0.7
60
0.7
0.1
0.
71
5.
XES
Baakenec
FOR
Sook
laged
Figure 34: Ablation opposite effects (N 000). Precision, Recall, and IoU effect identifi cation varying the two effects difference in the main structural causal model (fixing N 5 000). NES consistently replicates the main results, still overcoming the paradox of Exploratory Causal Inference.
Varying propensity score Finally, we repeat the main experiments (fixing treatment effect T 0.6 and sample size N {500,5 000)) varying the treatment assignment probability P(T = 1) (0.2, 0.4, 0.6, 0.8), i.e. propensity score with no dependence on the covariates being a Randomized Controlled Trial. We report the results in Figures 35 Once again, both NES and the other baselines replicate the findings described for the main experiments in Section 6 Particularly, NES consistently overcomes the Paradox of Exploratory Causal Inference, which is the case for the other baselines. The results are consistent and almost invariant with respect to P(T = 1), even if, as expected, edge values of the propensity score, e.g., 0.2 and 0.8, can slightly affect the method's efficiency.
2.1
6.74
0.4
608
(92)
[(T)
x12)
Baskoneei
FDR
Figure 35: Ablation unbalanced treatment assignment (N 500, 7 = 0.6). Precision, Recall, and loU in effect identification varying the treatment assignment probability with sample size N 500. NES consistently replicates the main results in all the regimes, still overcoming the paradox of Exploratory Causal Inference.
46

---

Published as a conference paper at ICLR 2026
100
0.7
1pm
(22)
x12]
NES
Beakeneck
FOR
Sooe
liged
Figure 36: Ablation unbalanced treatment assignment (N 000, 0.6). Precision, Recall, and IoU in effect identification varying the treatment assignment probability with sample size N 000. NES consistently replicates the main results all the regimes, still overcoming the paradox of Exploratory Causal Inference.
E.3 ADDITIONAL BASELINES
Finally, we further include here two additional non-trivial, still heuristic baselines to compare our method with. Particularly inspired by Causal Feature Learning (Chalupka al. 2017). which tempts to abstract effects by clustering with respect to P(T X z). we propose to consider additional neural effect selector obtained by regressing the treatment T on the SAE representation of X, and filtering only the relevant codes. The idea is that the (by design) non-visible treatment information is indirectly retrievable from the effect measurement, and that such information flows through the anti-causal path Y T.
LASSO.
We consider a sparsified logistic regression model (recall that T' is binary) with an & penalty to enforce sparsity the SAE coefficients. Given SAE codes Z IR Nxm and treatment labels T E 1)., logistic regression models
PT, Z,, B) (30 + 3) + exp -Bo - Ej ZiyB,)
(39)
and fits parameters by minimizing the penalized negative log-likelihood
3 = arg min SER
Σ To + (1-T;) log(1 p.)] + A11
(40)
where À 0 controls sparsity. The resulting selected neurons are {j B, 0).
Stasso
(41)
Stability-Selected LASSO. To mitigate instability due to correlated SAE codes, we additionally consider stability selection. Given fixed regularization strength (c.g.. tuned via cross-validation), we repeatedly refit the LASSO model on bootstrapped subsamples of the data. For each bootstrap iteration b 1,...,
.....,.. B, let ((0 be the fitted coefficients. We then define a stability score
B
I
Σ b=1
(00)
#0),
(42)
B
and select those neurons consistently appearing across many subsamples:
Saable where (0, 1) is high-confidence threshold. In practice, consider 0.6.
{j 11, 2 s).
(43)
We replicate once again the main experimental setup described Section additionally including
the two novel baselines, and report the results in Figure 37. Interestingly, the new baselines reach
47

---

Published as a conference paper at ICLR 2026
comparable performance to vanilla multiple- methods, despite explicitly exploiting the anti- causal path and never measuring the neural effect directly. With sufficient experimental power, they also reach full-effect recall, but-similarly to vanilla multi-testing- -till suffer from the Paradox of Exploratory Causal Inference. Indeed, we are not aware of any theoretical result guaranteeing that these heuristics should recover the standalone ground-truth affected outcomes among all candidate neurons, Stability selection appears to boost vanilla LASSO performance, and with sufficient power, these approaches slightly outperform vanilla multi-testing (although precision remains unsatisfac- tory, i.e., << 1).
62-
0.3
0.5
0.4
1.4
0.2
N
N
3.44
3.0
cosaco
5003
Bacierooo
C3L, (Lars))
vilio Bnows
Figure 37: Additional Baselines from Causal Feature Learning. Precision, Recall, and IoU in ef- fect identification, including two baselines inspired by effect abstraction in Causal Feature Learning using LASSO with without stability selection. NES consistently replicates the main results in all the regimes, still overcoming the paradox of Exploratory Causal Inference.
48


Reviews:
[{"review_id": "2iJWAxM4P1", "reviewer": "Reviewer_CiiA", "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.", "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?\n\n7. Why is it necessary to remap $X$ to a representation from the foundation model?\n\n8. 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?", "limitations": "", "rating": 4, "confidence": 3, "soundness": 3, "presentation": 2, "contribution": 2, "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.\n\n2. Experiments provide some interesting insight into the consequences of the proposed approach.", "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.\n\n4. Guarantees of the proposed approach are mostly leveraging mutual information between variables, but mutual information may not capture causal nuances between variables.\n\n5. The paper could be improved in clarity. Notably, it might help to include a figure of the whole pipeline or perhaps an example.", "quality": null, "clarity": null, "significance": null, "originality": null, "strengths_and_weaknesses": "", "was_revised": false, "final_justification": "", "rebuttal": "", "claims_and_evidence": "", "methods_and_evaluation_criteria": "", "theoretical_claims": "", "experimental_designs_or_analyses": "", "relation_to_broader_scientific_literature": "", "essential_references_not_discussed": "", "other_strengths_and_weaknesses": "", "other_comments_or_suggestions": "", "questions_for_authors": "", "summary_of_paper": "", "summary_of_recommendation": "", "technical_quality": "", "clarity_of_presentation": "", "potential_impact": "", "robotics_focus": "", "quality_of_limitations": "", "questions_for_rebuttal": "", "reasons_to_accept": "", "reasons_to_reject": "", "questions_to_authors": "", "extra_scores": {}}, {"review_id": "d9euCqYIaH", "reviewer": "Reviewer_ZiiZ", "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.", "questions": "**Q: Computing** v_k **when** Y **is unobserved.**\n\nIn 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?", "limitations": "", "rating": 8, "confidence": 4, "soundness": 3, "presentation": 3, "contribution": 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.", "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.", "quality": null, "clarity": null, "significance": null, "originality": null, "strengths_and_weaknesses": "", "was_revised": false, "final_justification": "", "rebuttal": "", "claims_and_evidence": "", "methods_and_evaluation_criteria": "", "theoretical_claims": "", "experimental_designs_or_analyses": "", "relation_to_broader_scientific_literature": "", "essential_references_not_discussed": "", "other_strengths_and_weaknesses": "", "other_comments_or_suggestions": "", "questions_for_authors": "", "summary_of_paper": "", "summary_of_recommendation": "", "technical_quality": "", "clarity_of_presentation": "", "potential_impact": "", "robotics_focus": "", "quality_of_limitations": "", "questions_for_rebuttal": "", "reasons_to_accept": "", "reasons_to_reject": "", "questions_to_authors": "", "extra_scores": {}}, {"review_id": "AEudDTuMV3", "reviewer": "Reviewer_rdaU", "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.", "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)\n\nWhen 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?\n\nOn 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.\n\nI 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.", "limitations": "", "rating": 8, "confidence": 2, "soundness": 3, "presentation": 2, "contribution": 4, "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.", "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.\n\nThe 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.\n\nMy 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)\n\nThe 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.\n\nI 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.\n\nWhile 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:\n- line 43: \"or more in general\" -> \"or more **generally**\"\n- line 46: \"modern science started embracing the creation of atlases\" -> \"modern science **has started embracing the creation of atlases**\n- line 48: \"(Weinstein et al., 2013), imaging of cells ...\" -> \"(Weinstein et al., 2013), **and** imaging of cells ...\"\n- 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\"?)\n- line 127: I think \"i.e., T has no causes\" should be in parentheses", "quality": null, "clarity": null, "significance": null, "originality": null, "strengths_and_weaknesses": "", "was_revised": false, "final_justification": "", "rebuttal": "", "claims_and_evidence": "", "methods_and_evaluation_criteria": "", "theoretical_claims": "", "experimental_designs_or_analyses": "", "relation_to_broader_scientific_literature": "", "essential_references_not_discussed": "", "other_strengths_and_weaknesses": "", "other_comments_or_suggestions": "", "questions_for_authors": "", "summary_of_paper": "", "summary_of_recommendation": "", "technical_quality": "", "clarity_of_presentation": "", "potential_impact": "", "robotics_focus": "", "quality_of_limitations": "", "questions_for_rebuttal": "", "reasons_to_accept": "", "reasons_to_reject": "", "questions_to_authors": "", "extra_scores": {}}, {"review_id": "22qsjviiUk", "reviewer": "Reviewer_waNL", "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.", "questions": "1.\tCan 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?\n2.\tWhat 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.\n3.\tHow 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?\n4.\tIn the ecology study, could you provide bootstrap confidence intervals for NES effect sizes on residualized codes, or permutation tests that respect the randomization?\n5.\tBeyond “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?\n6.\tCould NES results predict downstream manual labels or behavioral rates on an unseen experimental batch, thereby validating discovered effects?", "limitations": "", "rating": 8, "confidence": 4, "soundness": 3, "presentation": 3, "contribution": 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.\n\nQuality. 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. \n\nClarity. 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.\n \nSignificance. 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.", "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). \n\nNES 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). \n\nThe 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.\n\nThe 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.", "quality": null, "clarity": null, "significance": null, "originality": null, "strengths_and_weaknesses": "", "was_revised": false, "final_justification": "", "rebuttal": "", "claims_and_evidence": "", "methods_and_evaluation_criteria": "", "theoretical_claims": "", "experimental_designs_or_analyses": "", "relation_to_broader_scientific_literature": "", "essential_references_not_discussed": "", "other_strengths_and_weaknesses": "", "other_comments_or_suggestions": "", "questions_for_authors": "", "summary_of_paper": "", "summary_of_recommendation": "", "technical_quality": "", "clarity_of_presentation": "", "potential_impact": "", "robotics_focus": "", "quality_of_limitations": "", "questions_for_rebuttal": "", "reasons_to_accept": "", "reasons_to_reject": "", "questions_to_authors": "", "extra_scores": {}}]

Author rebuttal:

Decision: Accept (Oral)