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Under review as a conference paper at ICLR 2027

What Do Activation Interventions Establish? Causal Controls for Autoregressive Time-Series Foundation Models

Abstract

Time-series foundation models (TSFMs) are increasingly studied through interventions on their internal activations; such interventions are also proposed as practical tools, for example to steer a forecast toward a historical crash. When an intervention succeeds, what has it established? Success is usually measured by restoration, the fraction of the gap to a donor’s forecast that the edit closes, which shows only that the edited quantity can influence the forecast. It does not show that the effect continues after the edit stops, that the edited site is special, what carries the effect forward, or that the displayed change comes from the edit. We identify these four causal claims and introduce, to our knowledge, the first causal controls for them in autoregressive TSFMs: releasing the edit and scoring later steps, matched edits at other sites, replaying the emitted values in an unedited run and simplifying them, and an activation-by-scale factorial; two of them apply to any TSFM. With them, each claim can be tested rather than assumed. On Chronos-T5, each control changes what a successful intervention can be taken to show. On observed traffic and pedestrian series, an edit that removes 82% of the gap while active removes only 7% once it stops. On controlled synthetic series, where a four-step edit does persist (96%), the effect is carried by the emitted forecast values: collapsing them to their mean retains essentially all of the shape improvement, yet with a key–value cache, replay recovers only about 70% of an early-layer edit’s effect. In the six public Chronos cases of time2time, which reports steering forecasts between market regimes, a case-specific output rescaling produces the displayed direction in all six, while the activation transplant alone moves the median forecast the opposite way in five (three with intervals excluding zero), although it shifts tails and drawdowns toward the donor regime. A successful intervention establishes influence; each stronger causal claim requires the causal control that tests it.

Primary area:
interpretability and explainable AI
Keywords:
mechanistic interpretability, activation patching, causal interventions, causal controls, time-series foundation models, autoregressive forecasting

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_Zdg6OpenReview ↗
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2
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Informativeness
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Paper summary

This paper examines what successful activation interventions in autoregressive time-series foundation models (TSFMs) can establish beyond their immediate effects on model outputs. The authors identify four causal claims as persistence, location specificity, emitted-output sufficiency, and numerical attribution. They propose corresponding controls: release, matched-site interventions, replay and simplification of emitted values, and an activation-by-scale factorial analysis. Through experiments on Chronos-T5 using synthetic and observed time series, the authors show that high restoration does not necessarily imply persistence, that several terminal intervention sites yield comparable effects, and that persistent effects can propagate through emitted forecast values, with additional contributions from the key–value cache at upstream decoder sites. Furthermore, a reanalysis of six published Chronos steering cases reveals that output rescaling, rather than activation transplantation, determines the displayed median-level steering direction.

Critical strengths
  1. The paper addresses an important and underexplored problem in the interpretability of time-series foundation models. The distinction between intervention effectiveness and stronger causal claims is conceptually valuable.
  2. The experimental design is generally careful, incorporating controlled comparisons, paired sampling, fixed numerical scaling, and cluster-level uncertainty estimation.
  3. The time2time reanalysis is particularly insightful, revealing that output rescaling determines the displayed median-level steering direction in the examined Chronos cases, while activation transplantation influences tails and drawdowns.
Critical weaknesses
  1. The proposed controls are conceptually related to existing activation patching, causal mediation, and factorial ablation techniques. Their methodological novelty beyond adapting established approaches to autoregressive TSFMs could be clarified.
  2. Most findings are based on Chronos-T5, while experiments on Lag-Llama and Toto remain inconclusive, limiting evidence for cross-architecture generalizability.
  3. Some prespecified thresholds (e.g., restoration ≥ 0.5 and the ±0.10 equivalence margin) lack sufficient theoretical justification.
Questions for authors
  1. What are the main methodological distinctions between the proposed controls and existing approaches such as causal mediation analysis, activation patching, and factorial ablation?
  2. What explains the strong interaction between emitted tokens and cached internal states at early decoder layers? Can the authors provide further mechanistic insights into this interaction?
  3. What explains the strong interaction between emitted tokens and cached internal states at early decoder layers?
  4. Can you provide more justification or sensitivity analyses for the prespecified numeric thresholds (e.g., 0.50/0.30 for persistence, ±0.10 equivalence), and do the qualitative conclusions change under plausible alternatives?
  5. Could the authors elaborate on why the interventions on Lag-Llama and Toto failed to produce sufficiently strong active effects or persistent effects? Are these failures attributable to architectural differences, intervention-site selection, or other factors?
6 comments

Thank you for the careful reading and the specific questions.

In short. (1) Our controls build on standard intervention techniques (patching, mediation and factorial designs); a new table states what each builds on and what is specific to autoregressive TSFMs. (2) New analyses show that the early-layer interaction has structure by layer, attention head and position. We do not claim to know what the cached entries encode. (3) In a post-hoc check, both persistence verdicts are unchanged for every common threshold from 0.10 to 0.94. (4) We cannot attribute the Lag-Llama and Toto failures to a cause, and we now report them as boundary results.

What we have revised: a table relating each control to patching, mediation and factorial designs (Appendix A.3, Table 3); threshold sensitivity (Appendix A.4); the cache route in the main text (§4.4) with analyses by layer, head and position (Appendix B.10); other architectures stated as boundary results (§6 and Appendix D.1).

Q1: Relation to patching, mediation and factorial ablation. We do not claim to have invented these techniques. Each control is a specific use of one (new Appendix A.3, Table 3):

Our controlBuilds onWhat is specific to autoregressive TSFMs
ReleaseActivation patching with a time-limited patchLater forecasts are scored after the patch ends, so the patched state has to propagate through generation
Replay and simplificationCausal mediation (emitted values as mediator)The mediator is the model's own emitted forecast; collapsing it to its mean, or taking it from a wrong donor, tests what about it carries the effect
Cached-decoder crossingTwo-mediator factorialEmitted values and cached keys/values are crossed, separating the two routes and their interaction
Activation × scale factorialFactorial ablationOne factor is numerical output de-normalisation, which acts outside the network but decides the displayed direction

Transferring them required choices that language-model patching does not face: random draws are held fixed across runs, so that released, replayed and edited runs differ only in the edit; the edit is fully removed before later steps; and one factorial factor, de-normalisation, acts outside the network.

The contribution is turning these techniques into causal controls for TSFMs, and what that changes. For example, the factorial shows that the displayed median direction of a published Chronos steering result comes from output rescaling, not from the activation transplant. We also think the timing matters. Probing studies in language models adopted control tasks only after many claims had spread (Hewitt and Liang, EMNLP 2019); TSFM representation studies can build such controls in from the start. They are needed more here: steered text can be read and checked, but nobody can tell by looking whether a displayed change in a sequence of numbers came from the edit.

Q2–Q3: The early-layer interaction (we read these as one question). Short answer: we can show how the interaction is spread across the cache, but not what the cached entries encode, so we make no mechanistic claim.

The effect. At decoder layer 0 on synthetic series, the edited cache on its own adds nothing measurable (−0.012 [−0.045, 0.021]), but together with the edited emitted values it adds 0.278 [0.173, 0.388]. One hypothesis consistent with this, which our analyses do not test, is that later positions attend to cached keys and values that help only when the inputs follow the edited trajectory.

How it is spread. New analyses put pieces of the edited cache back into the replay run (§4.4, Appendix B.10):

  • By layer: no single layer recovers the whole effect; the largest share is at layer 5 (56%), and the layers overlap rather than add.
  • By attention head (layer 5, chosen after the layer result): no single head carries it; removing any one costs at most 4% of the gap.
  • By position: it sits mainly in the entries written at the three emitted-token positions.

Outside our own edits. In our adaptation of Wiliński et al.'s steering (Appendix D.2), cached decoder state again mattered beyond the emitted values at the paper's setting. On our observed pairs, the layer-0 comparisons are descriptive only.

Q4: Thresholds. The cutoffs are operational criteria fixed before each experiment, not externally validated margins, but each has a direct reading and a standard form. R ≥ 0.50 implies, in pooled distance, that the released forecast is no farther from the donor's forecast than from the recipient's own. The ±0.10 margin is one tenth of the way from no repair (0) to full repair (1), applied with the confidence-interval equivalence criterion (Lakens, 2017). The 75% bar follows the fraction-retention form of non-inferiority testing (Rothmann et al., 2003). These justify the form of each criterion, not its exact value. A post-hoc check from the saved estimates (new Appendix A.4) gives:

  • Persistence: the synthetic result passes and the observed-pair result fails for every common cutoff from 0.10 to 0.94, applied to both the estimate and its lower bound.
  • Matched sites: all three intervals lie within ±0.011, far inside the prespecified ±0.10 margin.
  • Mean-repeat retention: the lower end of its interval is 0.987, far above the prespecified 75% bar.

The original verdicts are unchanged.

These describe precision; they do not justify a particular margin, and failing a bar is not evidence of a zero effect.

W2 and Q5: Lag-Llama and Toto. We agree that our evidence beyond Chronos-T5 is limited. Limitations (§6) now says that all persistence and routing results are on Chronos-T5, and that our Lag-Llama and Toto writes either did not work while active or did not persist. We did not vary architecture, site or strength systematically, so we cannot attribute the failures to a cause. In the main experiments, a write at every step did not reach the required active effect, so persistence could not be tested. A separate Toto write worked while active but failed its persistence criterion after one edited step. And time2time's Toto transplant has a large active effect (−442.6 index points) with no rescaling. A working Toto intervention is therefore possible; whether its effects persist remains open.

If these answers address your concerns, we would be grateful if you would reconsider your score.

Reviewer_h7smOpenReview ↗
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Paper summary

In simple terms, a time-series forecaster like Chronos predicts the future one step at a time. At each new step, it feeds each prediction back in as input for the next step. Researchers who study interpretability of foundational models modify activations mid-computation to see what happens. For example, if a pasted internal state is from a "crash" period, the forecast will turn down, and that could mean that the model "understands" crashes. Time2time paper made exactly that claim.

The main point of this paper is what changes, exactly, when such an edit has been made? The paper argues that the edited quantity can influence the output while you are holding it there. This statement by itself is almost tautological, and this is why I have scored the paper's contribution lower. But this claim is not the paper's finding; it's the paper's floor - the point the authors start with, because the most recent literature in this area makes claims that are much higher than the floor. Claims range from governing predictions, which implies that the internal state carries the effect, to stress-testing, which implies persistence.

As stated, this paper makes four contributions. First, it shows that the displayed steering direction in time2time’s public Chronos cases comes from a hand-coded, case-specific output scaling that the time2time paper does not describe. This paper decomposes the displayed effect into scaling, transplant, and interaction terms. Second, it measures how fast a forced edit washes out: edits that persist on synthetic series do not persist to the same extent on real data. Third, it separates the two routes an edit can take through an autoregressive model - emitted values versus cached internal state. Fourth, the paper offers four controls (release, matched sites, replay, scale factorial) as a checklist for claims of persistence, location, sufficiency, and rescaling. The controls are not new - they are borrowed from LLM interpretability literature, but it appears that none of the TSFM intervention studies ran them, and the time2time reanalysis shows the cost of skipping them.

Critical strengths

The first main result is a verifiable correction of a published paper. The authors evaluate the public repository for the time2time model (Sanyal et al., 2025), reconstruct its six Chronos cases, and decompose the displayed effect into output scaling, activation transplant, and their interaction. The paper further shows that the steering direction reported by time2time is set by a hand-coded, case-specific scaling factor, which the authors do not describe. Moreover, they find that the transplant alone moves the median the other way in five of six cases. This is consequential because it is the kind of result that changes how a cited finding is used: anyone treating time2time as evidence that TSFMs encode regime concepts now has a specific, reproducible reason not to.

The second contribution is the measure of how fast a forced edit washes out: edits that persist on synthetic series do not persist to the same extent on real data. A four-step edit at the same site persists at 0.96 on synthetic drift series and at 0.07 after release on traffic and pedestrian pairs. This matters because the field’s stress-testing use case (“inject a regime and let the model run”) rests on persistence, and the paper is the first to quantify that on real series it does not hold for this model. The result is limited to Chronos-T5, which caps how much weight I give it, but within that scope it is clean, bootstrapped at the right unit, and reproduced bitwise.

Critical weaknesses

First, it was not clear to me why the authors decided to audit one paper, time2time (Sanyal et al., 2025). It's a NeurIPS workshop paper, cited three times in 13 months, so it's hardly a contribution that moves the field. Wilinski et al., (2025), which the paper cites, would have been a much stronger target if the same claims held for that study. With that, only half of the time2time was audited; the other half, with decoder-only Toto, "did not work while active." So what is completely unclear is whether other TSFM steering results have the same problem.

Second, the four claims and their controls are not new; the novelty is their transfer to TSFMs. The paper accurately cites the origins, and the paper’s framing (“the first causal controls for them in autoregressive TSFMs”) is accurate. But the contribution is an application, not a methodological advance. I don't know if such an application clears the novelty bar for ICLR.

Third, the synthetic persistence and sufficiency results, at least to me, appear to be close to definitional. The selected site is the final decoder MLP output, after the last attention layer. By construction, its only route to later steps is through emitted values. So the paper’s cleanest-looking numbers come from editing one specific place in the network, the output of the final MLP in the decoder, on synthetic series. The problem is that this site sits after the last attention layer. Nothing downstream can read it except the step that converts it into an emitted value. So when the paper shows that replaying the emitted values reproduces the edit’s effect exactly, that is not a discovery; it is forced by where the edit was made. In this case, replay equality is, as the paper says, “an implementation check.” The mean-repeat result has the same character. Four forced values at the forecast origin tell an autoregressive model the new level and slope, and the seasonal pattern is already in the 256 steps of history. So of course a crude version of those four values (their mean, repeated) does the job: there is nothing else for the edit to carry. The paper’s appendix confirms this: a prefix taken from the wrong donor, or a cyclically shuffled one, restores just as well. The mechanism is “any plausible four-token level shift,” not anything specific to the donor.

Fourth, the paper claims that their work is applicable beyond Chronos, but did not provide any verification beyond one model family. The paper’s controls need autoregressive decoding with a cache. As far as I know, Chronos T5 is the only encoder-decoder model that operates that way, and I doubt that results will be just as applicable to encoder-only or decoder-only models.

Fifth, presentation. The main paper is readable, but the appendix can be cut by at least a third. There is too much information about artifact codes, hash records, which runs were visible during development, etc. While complete transparency is welcome, the content gets lost behind the volume.

Questions for authors
  1. Can the factorial be run on the public Toto path of time2time? If the Toto pipeline also rescales outputs, the source’s main result is affected; if it does not, the Chronos finding is pipeline-specific and the abstract should say so.
  2. Did you contact the time2time authors about the hard-coded α values? Is there a documented rationale (an “intensity” parameter, say) that the public code omits?
  3. Why not center the study on the layer-0 and layer-4 residual sites, where the interventions are internal and the cache route is live, rather than on the final MLP?
  4. Can release be applied to one of the published Chronos steering interventions from Wiliński et al. (2025)? That would show whether non-persistence on observed data is general.
  5. For the observed pairs, how does released restoration vary with the magnitude of the level shift or ramp? Is there a regime where four tokens do persist on real data?
4 comments

Thank you. Your "floor versus higher claims" summary states our motivation better than we did: an edit that changes the forecast while held in place is the floor, and claims of persistence or of a state that governs predictions need more.

In short. You valued two results, the time2time correction and the washout on real series, and raised four concerns.

  1. Target: time2time is a case study of what goes wrong without the controls. In its public Chronos cases, the displayed steering direction comes from an output rescaling, not from the activation transplant. One case cannot show how common the problem is; it shows what skipping the controls can cost.
  2. Novelty: we agree the intervention techniques are standard; we turn them into causal controls for TSFMs, and applying them changes conclusions.
  3. Final MLP: the site forces exact replay, but not whether the edit persists. The same four-step edit at the same site restores 0.96 on synthetic series with Chronos-T5-Small, 0.70 on synthetic series with Chronos-T5-Base, and 0.07 on observed series with Chronos-T5-Small.
  4. Scope: our persistence and routing results are now stated as Chronos-T5 results. The time2time Toto path has no rescaling, so the rescaling finding is specific to its Chronos pipeline (now in the abstract). We also applied release to the published steering of Wiliński et al. on observed data, as our own adaptation with stated limits: in both steering settings, the forecast after release differed from continued steering (Q4).

What we have revised: Chronos-pipeline scope of the rescaling finding in the abstract and §5; the Toto path (Appendix C.2); release on Wiliński et al. (Appendix D.2); level-and-slope reading of the final-MLP results (§4.2); the layer-0 cache route in the main text (§4.4, Table 2) with layer, head and position splices (Appendix B.10); shift-magnitude analysis (Appendix B.5); Chronos-T5 scope in Limitations (§6); appendix cut from 17 to 12 pages.

Why time2time. It is a case study of what can go wrong without these controls, not a sample of the field. We chose it for two reasons. Its public code reproduces its six displayed Chronos cases exactly, so each displayed effect can be traced to its sources. And it proposes a use, stress-testing by steering toward a crash, that depends on the stronger claims. We do not claim that other steering results share the rescaling problem: it is specific to time2time's Chronos pipeline (its Toto path has none, Q1). Wiliński et al.'s released steering code has no output-rescaling step: it decodes with Chronos's standard output transform, using the recipient's own context scale in both the steered and unsteered runs. We read this code; we did not run it. So our Wiliński test (Q4) checks persistence, not rescaling.

W2: Novelty. Agreed: we did not invent patching, mediation or factorial designs. A new appendix table maps each control to its origin (Appendix A.3), and the abstract and first contribution now say that we turn these standard intervention techniques into causal controls. Our claim is different: running these controls on a TSFM changes conclusions that are currently drawn without them. As you note, the TSFM intervention studies we know of did not run them. On one model, each control overturns or bounds such a conclusion:

  • the factorial shows that the displayed median direction of a published Chronos steering result comes from output rescaling, not from the activation transplant;
  • release shows that, on 173 observed pairs, an edit restoring 0.83 of the gap while active keeps 0.07 once it stops, which undercuts the stress-testing use there;
  • replay and the cache analyses show that an edit can travel through cached state as well as through emitted values.

The transfer also required design choices that language-model patching does not face. Random draws must be held fixed across runs, so that released and replayed runs differ only in the edit. The edit must be fully removed before later steps. And one factor of the factorial is numerical de-normalisation outside the network. Adopting these controls before TSFM claims accumulate is cheaper than correcting them afterwards, as probing studies had to after Hewitt and Liang's (2019) control tasks. We see the paper as an empirical audit with reusable controls. Whether that clears the bar is your judgment.

W3: Final MLP. Agreed on two points. Exact replay at this site is forced by its position after the last attention layer, so it is an implementation check, as the paper says. And we agree with your reading of the mean-repeat, wrong-donor and shuffled-prefix results: what persists is consistent with a level and slope shift, not donor-specific detail; §4.2 now says so. What the site fixes is the route, not the outcome. If the architecture determined how much persists, the same four-step edit at the same site would give the same answer. It does not: 0.96 (90% interval [0.95, 0.97]) on Chronos-T5-Small synthetic series, 0.70 (one-sided 95% lower bound 0.626) on Chronos-T5-Base synthetic series, and 0.073 (90% interval [0.054, 0.096]) on 173 observed pairs with Chronos-T5-Small. Whether an edit persists, and how much, is an empirical result that release measures.

W4: Beyond Chronos. Agreed: a portable question is not a general result. The revision states that our persistence and routing results are on Chronos-T5, and the abstract now separates the controls, which can be run on any autoregressive TSFM, from these results. The controls do not need a cache: release and replay need only emitted values that re-enter as inputs (singly or in blocks), and only the cached-decoder variant needs a cache. Decoder-only models qualify: our separate Toto study applied release. Matched edits and the scale factorial need no autoregression, so they can also be run on encoder-only models. Our other-architecture evidence marks boundaries: our main Lag-Llama and Toto writes did not reach the required active effect, and a separate Toto write worked while active but failed its persistence criterion after one edited step.

W5: Appendix. The appendix is now 12 pages instead of 17. Hashes, run logs and verification records moved to the evidence package. We kept, in one sentence each, the disclosures that bear on how far a result can be trusted, such as which outcomes were visible before a specification was fixed; we can move these too if you prefer. Each experiment keeps its question, design, controls, results and limitations.

Q1: Toto path. On the released 2017-calm recipient / 2008-crash donor case, the answer is your second branch. The Toto path has no output rescaling: forecasts are de-normalised with the recipient's own location and scale in every run. Within the source's execution path, the transplant itself moves the final-step median by −442.6 index points (95% interval [−469.6, −424.1]; all three sampling seeds agree), in the displayed crash direction. That is most of the displayed −640.0; the remaining −197.4 comes from the source's custom execution path, not the transplant. The scaling finding is therefore specific to the Chronos pipeline, and the abstract, §5 and a new Appendix C.2 now say so. This does not settle the source's stronger reading, that the result shows a semantic crash concept: no control with random or wrong-regime statistics is reported, and a moved forecast establishes influence, not a concept. Qualifications: this is one case, the only displayed Toto case in the public code; the saved samples replay exactly, and we cannot verify the authors' checkpoint revision or random draws.

Our earlier statement that Toto "did not work while active" referred to our own write-and-release interventions, not to time2time's transplant. The revision separates the two.

Q2: Author contact. We did not contact the authors. We will ask them after the review period and report any rationale. The paper, README and code give none for the six values. They appear as an uncommented list, alphas=[0.1, -0.2, -0.1, 0.2, -1.8, -0.4], used as alpha*style_scale + (1-alpha)*content_scale; negative values move the scale away from the donor. We report what the code does, reproduced exactly in all six cases, without inferring intent.

Q3: Layers 0 and 4. The final MLP was the only one of 30 screened outputs to pass the prespecified 0.90 screen (next best 0.074). We agree the internal sites belong in the main text; §4.4 now presents them. At decoder layer 0 on synthetic series, release restores 0.871 and replay 0.605 (gap 0.27 [0.18, 0.35]). The edited cache alone adds −0.012 [−0.045, 0.021], but 0.278 [0.173, 0.388] in interaction with the emitted values. At layer 4 the gap is 0.018 [0.003, 0.033]. New splices show this internal route has structure: the cache contribution is spread over attention heads and concentrated in the entries written at the emitted-token positions (Appendix B.10). On observed pairs, release stays at 0.07–0.12 at all three sites after a four-step edit (Table 5). These comparisons are descriptive, because the continuous edit at layer 0 did not reach its 0.90 criterion there.

Q4: Wiliński et al. (2025). They do not test what happens after steering stops, so this is our own extension, and our own adaptation of their steering rather than a reproduction of their experiment. We used Chronos-T5-Large on 120 observed traffic series. Three results:

  • While steering is on: with the steering strength in their released script, the forecast trend moved opposite to the intended direction; with the setting in their paper, it moved as intended. This does not refute their results.
  • After steering stops: in both settings, the forecast differed from what continued steering would give. With the paper's setting, it went further: the trend ended below the unsteered forecast, on the opposite side from the steering (−0.24, interval [−0.32, −0.18]). With the steering strength in their released script, the difference from the unsteered forecast was +0.05 [−0.09, 0.17]; this interval includes zero, which does not show that the effect is gone.
  • What carries the effect: with the paper's setting, the model's internal cached state matters, not only the forecast values it has already produced.

Limits: one model checkpoint, five possibly dependent time periods, and steering vectors we fitted ourselves. Numbers and intervals are in the new Appendix D.2.

Q5: Magnitude. We split the 173 pairs by dataset × regime and then by tertiles of the detected shift or ramp size, giving 12 exploratory subgroups. Four-step released restoration ranges from −0.006 to 0.125, all far below the 0.40 bar. Only pedestrian ramps rise (0.054 → 0.055 → 0.088). Longer edits do not rescue persistence: on steps 17–32, restoration rises from 0.01 (one step) to 0.17 [0.13, 0.21] (16 steps), against 0.84 for continuous writing. The scan is post hoc, and the pedestrian pairs share one connected set of source series, so it cannot rule out persistence in other regimes or datasets. It is now reported in the appendix.

If these revisions address your concerns, we would be grateful if you would reconsider your score.

Thank you again for your detailed review. We hope the new analyses you asked for (the Toto path, release on Wiliński et al., the internal sites and the shift-magnitude split) address your questions. If any point remains open, we would be glad to respond before the discussion period ends on 18 November.

Reviewer_8av7OpenReview ↗
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Confidence
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Informativeness
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Paper summary

My understanding is that the paper proposes causal controls to interpret activation interventions in autoregressive time-series models. These controls assess whether an intervention’s effect persists after it is withdrawn, is specific to the modified component, and can be reproduced using the generated outputs alone. However, the broader motivation and the specific contribution of this framework remained unclear to me.

Critical strengths

The paper examines the effect of activation interventions on time-series foundation models, focusing on Chronos-T5 and a reanalysis of the public time2time Chronos pipeline.

Critical weaknesses
  • Unfortunately, I had difficulty understanding the paper. Its main objective remained unclear to me despite several readings.
  • In particular, I found it difficult to understand how the causal controls relate to the paper’s main contribution. A clearer explanation of what persistence, location specificity, emitted-output sufficiency, and numerical attribution are intended to establish in time-series models would be helpful. A concrete example linking an intervention, its corresponding control, and the conclusion drawn would make this discussion easier to follow.
  • The paper would benefit from careful proofreading. Some sentences are too long and could be shortened to improve clarity.
  • Some ideas could be expressed more precisely using mathematical equations, accompanied by clearly defined notation and intuitive explanations.
  • The bibliography includes 11 references to arXiv preprints. Could the authors check whether these papers have since been published in peer-reviewed venues and update the references accordingly?
Questions for authors

Please see the Weaknesses section.

4 comments

Thank you for reading the paper several times and telling us where it failed you. We rewrote the presentation, not only details.

In short. We rewrote the paper for clarity; the list below says where. The paper's point is this. An activation edit that changes a forecast shows only that the edit can influence the forecast. We test four stronger claims on Chronos-T5. Each control changes what a successful edit can be taken to show, including for one published steering result. If you have time for one pass, we suggest the abstract's last sentence, Table 1 (p. 4) and Figure 1 (p. 5), in that order; together they state the whole argument.

What we have revised: objective stated in one sentence (abstract, §1); worked example as Figure 1B–C (p. 5); Table 1 maps each claim to its control and result (p. 4); restoration equation (§3) and factorial equation (§5, p. 9); long sentences split and terms defined at first use throughout; bibliography corrected.

Objective. When an edit to a model's internal activations changes a forecast, we ask which further conclusions that success supports, and we test each one. That the forecast changes while the edit is held in place is only the minimum. Four stronger claims are often drawn from it, and each needs its own control:

  • Persistence: the effect continues after the edit stops, as calling an edit a stress test implies. Control: stop the edit and score the later steps.
  • Location specificity: the edited site is special. Control: make the same edit at other sites.
  • Emitted-output sufficiency: the forecast values the model has already produced carry the effect forward, not some lasting internal state. Control: feed those values into an unedited run.
  • Numerical attribution: the displayed change comes from the edit, not from other processing such as output rescaling. Control: apply the edit and the rescaling separately.

Table 1 gives each claim's criterion and result.

Worked example (new Figure 1B–C). Chronos forecasts one step at a time and feeds each forecast back as input. We copy a donor series' internal state at one site into a recipient series' run. The numbers below pool all 173 observed pairs (panel C).

  • Intervention: copying at all 32 forecast steps restores 0.831 of the gap to the donor's forecast on steps 5–32.
  • Tempting conclusion: the copied state carries the donor's behaviour, so a brief injection should steer the forecast.
  • Control (release): copy at steps 1–4 only, then score steps 5–32: 0.073 (90% interval [0.054, 0.096]).
  • Conclusion: on these 173 pairs, the edit works while active but leaves little trace once it stops.

Panel B shows one of these pairs (0.86 and 0.08). The abstract's 82% is the same continuous edit scored on all 32 steps. Table 1 applies the same template to all four claims: each claim, the control that tests it, the prespecified criterion, and the result.

What is new. Three findings on Chronos-T5:

  1. A published steering result (time2time) gets its displayed direction from an undocumented, case-specific output rescaling, not from the activation edit (all six public Chronos cases).
  2. Persistence must be measured. A four-step edit persists on synthetic series (0.96) but leaves little trace on 173 observed traffic and pedestrian pairs (0.073).
  3. An edit's effect can travel by two routes: through the emitted forecast values, or through the model's cached internal state. At an early layer on synthetic series, with a key–value cache, replaying the emitted values alone recovers only about 70% of the effect.

Why now. A drug trial includes its placebo arm from the start; it does not add one after the drug is on the market. Language-model interpretability added its controls late: probing results spread before Hewitt and Liang (EMNLP 2019) showed that high probe accuracy can reflect what the probe itself learns. TSFM representation studies can include these placebo arms from the start. They are also needed more here. Steered text can be read and checked. A forecast is a sequence of numbers, and nobody can tell by looking whether a displayed change came from the edit. time2time shows the cost: in its Chronos cases, the displayed direction came from an output rescaling that the plots cannot reveal.

Equations. In the revision, §3 defines restoration (Eq. 1): R = 1 − (distance from the edited forecast to the donor's forecast) / (distance from the unedited forecast to the donor's forecast), with distances summed over the scored steps. Its reading: 1 means the edited forecast matches the donor's, 0 means no change from the baseline, and negative values mean movement away. Released restoration is the same ratio on the steps after an m-step edit. The donor forecast is a model-generated target, not the observed future. §5 defines the four factorial forecasts (baseline, transplant-only, scale-only, joint) and gives the exact decomposition as an equation, with each term labelled: joint change = scale-only + transplant-only + interaction.

Writing. We shortened long sentences, checked that technical terms are defined at first use, and moved audit records (hashes and run logs) to the evidence package.

Bibliography. Of the 11 arXiv-only entries:

  • 5 have published versions, now cited: Chronos (TMLR 2024), TimesFM and Moirai (ICML 2024), the Monash archive (NeurIPS 2021 Datasets and Benchmarks), and Kalnāre et al. (IJCCI 2025, Springer CCIS 2026).
  • 2 are workshop papers, now labelled as such: Mishra (ICLR 2026 workshop) and the earlier Lag-Llama version (NeurIPS 2023 R0-FoMo workshop).
  • 4 remain preprints: the Toto technical report, path patching (Goldowsky-Dill et al.), the activation-patching guide (Heimersheim and Nanda), and Jander et al.

Soundness. We were not sure which aspect lowered the soundness rating, so we list the checks we think bear on it. Every confirmatory criterion was fixed before its experiment was run. Intervals come from resampling whole units (a synthetic construction or an observed pair), not single forecasts. Our re-run of the public time2time code reproduces its six displayed Chronos cases exactly. In a post-hoc check, both persistence verdicts are unchanged for every common threshold from 0.10 to 0.94 (Appendix A.4). We would gladly address any specific concern.

If the worked example and the rewrite address your concerns, we would be grateful if you would reconsider your score.

Thank you again for your review. We hope the revised PDF, in particular the worked example in Figure 1 and the claim-by-claim summary in Table 1, makes the paper’s objective clearer. If anything is still unclear, we would be glad to clarify before the discussion period ends on 18 November.

Thank you for the detailed response. The worked example and the claim-to-control mapping help clarify the paper’s objective and address my main presentation concerns.

Having considered your response and the broader discussion, I better appreciate the empirical contribution. However, I share the concerns about limited methodological novelty and the concentration of the main evidence on Chronos-T5, despite the useful additional analyses and more carefully stated limitations.

My remaining reservations concern the significance and generalizability of the contribution rather than a specific fundamental technical flaw. While the rebuttal improves my assessment, I maintain my original score.

Comments on the paper

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AuthorsOpenReview ↗

Summary of the discussion for the Area Chair

Dear Area Chair,

All three reviewers have replied, and we thank them. In brief:

  • No final reply raises a correctness issue. Reviewer 8av7's remaining reservations concern "the significance and generalizability of the contribution rather than a specific fundamental technical flaw." Reviewer h7sm raised their soundness score to 3.
  • The remaining objections are scope, novelty and significance: the main evidence is on Chronos-T5, and the controls build on established techniques. We agree with both facts, and the revised paper states them plainly.

Our argument: controls should come before cross-architecture claims.

Intervention studies of TSFMs are starting to be used for representational claims: that a model encodes a market regime, or that its internal states govern its forecasts. This is the moment to establish what such a claim requires, before these findings are cited and built on. Our time2time reanalysis shows what is at stake. In all six public Chronos cases, a case-specific output rescaling produces the displayed steering direction, and the activation transplant alone moves the median the opposite way in five. Reviewer h7sm’s initial review called this “a verifiable correction of a published paper.”

Mechanistic interpretability of language models went through the same early stage, and ICLR published several of these studies. Early work examined a single model or small models trained on toy tasks: a circuit for indirect-object identification in GPT-2 small (Wang et al., ICLR 2023), grokking in small transformers trained on modular arithmetic (Nanda et al., ICLR 2023), and board-state representations in a sequence model trained on Othello (Li et al., ICLR 2023). Papers on what patching results do and do not establish followed (Hase et al., NeurIPS 2023; Makelov et al., ICLR 2024; Zhang and Nanda, ICLR 2024).

TSFM interpretability is at an even earlier stage, and it is harder. A language model outputs text, so a person can read whether an edit changed what the model says. A TSFM outputs numbers. Whether an edit carries a concept such as “crash” has to be inferred from the forecast, and, as time2time shows, rescaling the output alone can produce the displayed direction.

We understand why the reviewers ask for cross-architecture conclusions. But we think the field is better served by clear controls for what it takes to establish each claim than by cross-architecture claims made before those controls exist, which risk the kind of problem we found in time2time. Whether this clears the bar for ICLR is your judgement, and we thank you for your time.

To the reviewers: this summary is visible to you as well. If we have left out or misstated anything you said, please add to it or correct it here.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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