acceptodds
Under review as a conference paper at ICLR 2027

When Backdoors Meet Selective State Spaces: Mechanisms and Attacks in Mamba Language Models

11 views

Abstract

Textual backdoor attacks have been extensively studied for attention-based natural language processing (NLP) backbones, but their behavior in selective state-space language models remains unclear. We investigate how backdoors are activated in Mamba, where trigger information must be written into a recurrent state, preserved through subsequent updates, and exposed at the classifier readout. Across four datasets, we compare Mamba and Pythia at two model scales under BadNL, SynBkd, StyBkd, and BGMAttack. The results show that architecture and scale jointly shape backdoor vulnerability: Mamba achieves higher clean accuracy at small scale, while larger models make non-lexical triggers substantially more reliable. Mechanism analysis further reveals that Mamba backdoors are readout-aligned and partially concentrated at the classifier interface.The input-dependent time step is a strong diagnostic of triggered computation and attack success, whereas component replacement identifies the mixer, gate, scan-output, and state-write pathways as the causal drivers. Guided by this insight, we propose Trigger-Aware State-Write Boosting (TASWB), which strengthens trigger-aware state writes and target-class margins. Together, our findings provide the first systematic study of Mamba backdoor activation and expose a state-write-mediated attack surface in selective state-space language models.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Textual Backdoor Attacks, Mamba, Selective State Space Models, Backdoor Mechanism Analysis, Trigger Activation

Reviews

Among:
Shape:
1234this paper, Top 1%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.50 over 2 reviews, above 99% of the others.
Reviewer_rhEqOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper investigates textual backdoors in Mamba language models through comparisons with Pythia across model scales, datasets, and trigger families. It examines how trigger position and classifier pooling affect activation, distinguishes linearly decodable trigger information from successful target prediction, and uses activation replacement to study Mamba components.

Critical strengths
  1. The paper goes beyond reporting ASR by examining trigger position, pooling, representation separability, and component interventions. In particular, distinguishing a diagnostic delta signal from an effective intervention point provides a useful perspective on backdoor analysis.

  2. The evaluation spans multiple trigger families and model scales, while the paired-token controls expose cases where high ASR reflects non-specific target drift. These analyses help qualify conclusions that would otherwise rely on aggregate attack success alone.

Critical weaknesses
  1. The interventions do not sufficiently isolate backdoor-specific state propagation from readout effects. Most component replacements concern an appended trigger that is itself the readout token, while state-write replacement produces 45.2% broken predictions. Stronger matched-token and head-trigger controls are needed to substantiate the claimed mechanism.

  2. TASWB’s contribution is not adequately separated from generic poison-loss reweighting. On binary IMDB, its per-example margin loss reduces to cross-entropy on poisoned examples. Without matched reweighting baselines and comparisons at comparable clean accuracy, the gains in Figure 4 do not clearly establish the benefit of the proposed state-write strategy.

Questions for authors

See Weaknesses.

3 comments
AuthorsOpenReview ↗

Response to Weakness 1 (state propagation vs. readout effects)

We thank the reviewer for this insight. Our original append-trigger interventions could not separate backdoor-specific state propagation from readout effects. We ran the suggested matched-token and head-trigger controls and will include all results.

1. Matched-token controls on the original append model. We introduced three control tokens (bb, dd, cc) that, like cf, are two lowercase letters tokenized as a single token, so token count, body tokens and final position match exactly. On the append model, these controls themselves yield 91.5–96.6% target predictions (vs. 99.2% for cf; n=377n=377 non-target examples), and replacing the trigger-position write with a matched donor leaves ASR at 95.5–98.4%. We therefore acknowledge that the append model lacks token specificity relative to these controls, and that the clean→cf replacements in Table 2 partly reflect changes to the readout token itself. The 45.2% Broken rate (34.5% on non-target examples) also shows that replacing wtw_t is disruptive rather than clean, so we will no longer present it as evidence of a backdoor-specific pathway.

2. New head-trigger model with non-readout interventions. We trained a plain BadNL model with cf at the head of the input (Mamba-130M, AG News, 5% poisoning, standard CE, no TASWB). It is trigger-specific: clean accuracy 92.2%, cf ASR 99.7%, while bb/dd/cc give only 9.3%/4.0%/6.4% target predictions. Triggered and control inputs differ only in the head token. At a downstream body position t=τ+kt=\tau+k, we replace the recurrent state with s~t=(1−λ)strecip+λstdonor\tilde s_t=(1-\lambda)s_t^{\text{recip}}+\lambda s_t^{\text{donor}}, taking the donor state from a matched input, and let the scan continue normally. We use k∈{8,32,64}k\in\{8,32,64\}, which lies beyond the local convolution window and at least 16 tokens before the readout, so the readout token is never modified. Specificity is

Spec=Δm(ctrl→cf)−Δm(ctrl→ctrl′),\mathrm{Spec}=\Delta m(\text{ctrl}\to\texttt{cf})-\Delta m(\text{ctrl}\to\text{ctrl}'),

i.e., the target-margin drop on triggered inputs minus that of a control swap at the same site. An exploratory layer scan pointed to layer 19 (0-indexed). We then fixed the configuration (L19, k=32k=32, λ=1\lambda=1) before evaluating on 281 new non-target texts that are disjoint from all earlier data. Margin CIs come from a paired bootstrap, and rate CIs are Clopper–Pearson intervals.

L19, k=32k{=}32, n=281n{=}281Target rateTrue-label acc.Broken
control → cf100% → 43.4–65.8%33.5–54.5%0.7–2.1%
cf → control5.7–10.0% → 83.3–85.1%15.0–16.7%0.0%
control → control5.7–10.0% → 5.7–7.8%85.8–88.6%Δacc −2.1 to +1.8 pp

(Ranges are over the three control tokens.)

  • Specificity: 6.57 [6.26, 6.87] (trigger drop 6.59 vs. control drop 0.02). It holds at k=8/64k=8/64 (6.76/6.17) and on 178 independent general-length texts (5.89 [5.51, 6.29]). It is small at neighbouring layers 18/20 (0.31/0.18).
  • Recovery rather than breakage: the ASR drop mainly turns into true-label recovery, with Broken at only 0.7–2.1%. Append write replacement, by contrast, gave 34.5–45.2%.
  • Reverse and graded effect: injecting the triggered state into control inputs, which contain no trigger, raises target predictions monotonically for λ∈{0,.25,.5,.75,1}\lambda\in\{0,.25,.5,.75,1\}: 7.6% → 41.3% → 59.6% → 74.3% → 84.3% (averaged over controls).

The inputs differ only in the head token, the intervention happens strictly before the readout, and the readout token is identical across conditions. These effects therefore cannot come from directly modifying the readout token. They support a causal contribution of the propagated recurrent state to the backdoor.

3. Revisions to our claims. We thank the reviewer for prompting more precise claims. (i) In the head model, no single-layer replacement of the trigger-position write wτw_\tau reduced ASR. We therefore no longer claim that state-write is a selective causal switch, and we will describe wtw_t only as a sensitive pathway. (ii) Forward suppression has a threshold: ASR stays ≥98% for λ≤0.75\lambda\le0.75. Matched control swaps also cause small but non-zero accuracy changes. We will report both. (iii) Layer 19 was identified by an exploratory scan before the independent confirmation, so we will not claim a unique or minimal single-layer mechanism.

Accordingly, in the abstract, the contributions and Sec. 4, we will replace "causal drivers" with "a causal contribution of propagated recurrent state in the evaluated head-trigger setting". The appendix will add the full head-trigger analysis, the matched-token append results, both Broken denominators, and all layers, positions and doses.

We hope these additions address the reviewer's concern, and thank the reviewer again for helping make our analysis more rigorous.

AuthorsOpenReview ↗

Response to Weakness 2 (TASWB vs. generic poison-loss reweighting)

We sincerely thank the reviewer for this valuable comment. The reviewer is correct. With μmin⁡=0\mu_{\min}=0 and two classes, softplus(−μi)=CE(oi,y⋆)\mathrm{softplus}(-\mu_i)=\mathrm{CE}(\mathbf{o}_i,y^\star). For a micro-batch of bb examples, kk of them poisoned,

LCE+λLmargin=1b[∑cleanCEi+(1+λbk)∑poisonCEi],\mathcal{L}_{\mathrm{CE}}+\lambda\mathcal{L}_{\mathrm{margin}}=\frac{1}{b}\left[\sum_{\mathrm{clean}}\mathrm{CE}_i+\left(1+\frac{\lambda b}{k}\right)\sum_{\mathrm{poison}}\mathrm{CE}_i\right],

so Lmargin\mathcal{L}_{\mathrm{margin}} is exactly poison-loss reweighting, not Mamba-specific, and the original Figure 4 could not isolate the state-write contribution.

1. Revised definition. TASWB will now consist only of the state-write objective, L=LCE+λwriteLwrite\mathcal{L}=\mathcal{L}_{\mathrm{CE}}+\lambda_{\mathrm{write}}\mathcal{L}_{\mathrm{write}}. We will present Lmargin\mathcal{L}_{\mathrm{margin}} only as a generic poison-loss reweighting baseline. The question then becomes: does Lwrite\mathcal{L}_{\mathrm{write}} add attack gain beyond this baseline at comparable clean accuracy?

2. Matched reweighting sweep. Setup: IMDB, Mamba-130M, head BadNL cf, 1% poisoning (100/10,000). All runs share poisoned data, data order, seed, LoRA and schedule, and use the epoch-5 checkpoint. We sweep the baseline LCE+λLmargin\mathcal{L}_{\mathrm{CE}}+\lambda\mathcal{L}_{\mathrm{margin}} over λ∈0.01,0.03,0.1,0.3,0.5\lambda\in\\{0.01,0.03,0.1,0.3,0.5\\}. At each λ\lambda, a paired run only adds Lwrite\mathcal{L}_{\mathrm{write}} (λwrite=1\lambda_{\mathrm{write}}=1 as in the paper, untuned). We use 1,000 validation examples; ASR uses the 500 non-target ones. Δ\Delta = (+write) − baseline, with 95% CIs from 20,000 paired stratified bootstrap resamples. Pure CE on the same poisoned data gives 87.0/14.8.

λ\lambdaBaseline CACC/ASR (%)+Lwrite\mathcal{L}_{\mathrm{write}} CACC/ASR (%)Δ\DeltaCACC (pp)Δ\DeltaASR [95% CI] (pp)
0.0187.0 / 15.087.4 / 17.6+0.4+2.6 [1.2, 4.2]
0.0387.2 / 15.687.3 / 19.0+0.1+3.4 [1.8, 5.2]
0.186.8 / 17.886.6 / 22.0−0.2+4.2 [2.4, 6.2]
0.385.2 / 26.084.6 / 35.2−0.6+9.2 [6.8, 11.8]
0.584.1 / 30.283.4 / 41.2−0.7+11.0 [8.2, 14.0]
  • Gain beyond the baseline: the write term raises ASR at all five weights, and no CI includes zero. In the original λ=1\lambda=1 setting, ASR rose 41.4%→55.6% (CACC 81.5%→82.2%).
  • Operating points at similar clean accuracy: at λ=0.03\lambda=0.03, CACC is 87.2% vs. 87.3% and ASR increases by +3.4 pp. For λ≤0.1\lambda\le0.1, both families stay within 0.5 pp of pure CE.
  • Equal-budget tuning: each family picks its highest-ASR λ\lambda from the same grid under a pre-fixed CACC constraint. With CACC ≥\ge 86.5% (pure CE − 0.5 pp), both families select λ=0.1\lambda=0.1: ASR goes from 17.8% to 22.0% and CACC from 86.8% to 86.6%. With CACC ≥\ge 87.0%, both select λ=0.03\lambda=0.03 (+3.4 pp ASR, +0.1 pp CACC).
  • Not due to already-misclassified inputs: on non-target examples both models classify correctly when clean, Δ\DeltaASR is +3.5 [1.6, 5.5] pp at λ=0.03\lambda=0.03 and +4.5 [2.4, 6.6] pp at λ=0.1\lambda=0.1.
  • At λ≥0.3\lambda\ge0.3 gains are larger but CACC falls below 86.5%; we treat these as a different trade-off, not comparable-utility evidence.

3. Revisions. In the abstract, contributions and Sec. 6, we will (a) define TASWB as Lwrite\mathcal{L}_{\mathrm{write}} and present Lmargin\mathcal{L}_{\mathrm{margin}} as the reweighting baseline, including the equivalence above; (b) replace Figure 4 with ASR–CACC curves for both families over λ\lambda, with numbers, CIs and control-prefix rates; and (c) state the claim as: in the current experimental setting, the TASWB write term provides additional attack gain beyond the margin baseline, and there are operating points with comparable clean accuracy.

We are grateful to the reviewer for pushing us to separate these effects; we believe the revised framing states TASWB's contribution more accurately.

Thanks for your reply. I have updated the rating. Good Luck!

Reviewer_6KG6OpenReview ↗
Rating
4(+2)
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper is very interesting, it’s a mechanistic interpretability paper on backdoors applied to a Mamba model. They test several backdoors (different triggers and behavior classes) and study how the trigger mechanism propagates within the mamba architecture. They contrast with a transformer-based model, Pythia, essentially as a control model and not as a different architecture-mirror of all their mechanistic analysis.

They somewhat convincingly identify the component responsible for the trigger propagation. They demonstrate this by proposing a way to reinforce the backdoor effectiveness at training time (their TASWB training objective[1]).

Given the amount of experiments and ablations, I had troubles to really follow what they did so I made a quick formalization :

A backdoor B can be defined by a tuple <T, bV> where T is the trigger and bV the behaviour activated by this trigger. In this paper, they add a third component, M, the model, that can be defined itself by its architecture, size, training data, etc. Let’s just say M=<A,S> with A the architecture and S the model size. The authors only used Lora as the backdoor training regime (which we call R) and varied the proportion of the data poisoning samples for some experiments (D). So essentially, they worked within a framework F (sorry for the alphabet listing) where F=<B,M,R,D> where they used one training regime R={Lora} and mostly focused on M={Mamba, Pythia}, , D={5%}, S={130M,160M parameters) and B={BadNL, SynBkd, StyBkd, BGMAttack}*, with M={Mamba} as their main model of their component-level causal analysis and B={BadNL} being the main focus of the mechanistic experiments (section 5) and the backdoor the authors targetted for optimisation with their proposed TASWB training objective (section 6, see [1]) (which could be seen as another training regime, leading to the framework F1=<M{mamba},D{1%},S{130M},B{badNL},R{TASWB}>)

So even though the authors did not test all configurations, they tested all backdoors with the classification behaviour in both size configurations, the fixed output prediction behaviour being only used with the large model size (>2.5B) in a Q&A scenario.

The authors' results suggest that Mamba is better at propagating early-position triggers to the classifier readout, while Pythia is more sensitive to triggers near the end of the input; they also found that Mamba's backdoor effects are concentrated in fewer classifier-input dimensions. Their component interventions implicate Mamba's gating, mixing, and state-write pathways, giving the authors credible causal evidences that Mamba's internal components participate in backdoor activation. The TASWB experiments give additional support for the usefulness of re-enforcing state writes.

Despite the relative narrow scope of the TASWB experiments (and the shortness of its dedicated section), I really appreciated this paper, to me it’s one of the rare cases where an interpretability paper goes beyond the "autopsy" of a model and tries to build on it to demonstrate the reliability of one of their findings. In all cases, I think that the criticisms I’ll give below can be solved during the rebuttal section, this is why my current assessment will be VOLUNTARILY low so I can improve it based on their responses.

Note to the authors: This is to encourage you, not to “kill” your paper, really.


Note: I have increased my overall assessment, the authors did a good job answering my criticisms, especially on the ethic part and the reasons they focused on the lexical trigger.

[1] TASWB (Trigger-Aware State-Write Boosting) is a training objective that strengthens the contribution of trigger tokens to Mamba’s recurrent state. The goal is to preserve their influence until the final classifier readout. It combines a state-write amplification loss with a target-class margin loss to improve backdoor attack success.

*BadNL= a fixed lexical trigger backdoor, SynkBD = a fixed syntactic structure trigger backdoor, StyBkd= a specific writing style trigger backdoor and BGMAttack a backdoor whose trigger relies on statistical patterns produced by a “black box” model that was asked to paraphrase content (a bit like the patterns used by LLM-content detector). All these backdoors were used in two behavior scenarios : rigged classification (4 classes news topic classification, 2 classes: movie reviews and 5 classes: lyelp) and fixed output prediction (Squad, must output “the question is too hard”)

Critical strengths
  • The paper studies, withing an extensive experimental setup, an interesting and relatively unexplored problem so far, how backdoors operate inside Mamba models. It made me wanted more from them: how could they generalize beyond architectural specificities. Many works have been published on Transformers and backdoors, there seems to be something more transversal to explore.

  • I liked how the authors went beyond probing by performing causal interventions on Mamba's internal components. I also really appreciated how they used their findings to design TASWB. As I said, they went beyond the “autopsy” paper.

Critical weaknesses

(sorry i've put 3 weaknesses and not 2 because the last one is more meta tbh)

** As I said above, the authors could have not tested every configuration, yet their experimental protocol is somewhat limited. They relied on LoRA fine-tuning, with different adapted modules for Mamba and Pythia. I would have liked to see whether their findings hold under full fine-tuning. On the same vein, most of the mechanistic experiments focus on a single lexical trigger (cf), a single behavior and the smaller models, which kind of limits the generalisation of their results (what happens with a different behavior?)

** I don’t understand why some experimental details are missing. Space is not scarce in the appendix section, right ? it makes the results difficult to reproduce. For example, the authors don't specify which generative model was used for BGMAttack, or which target labels were selected for the classification tasks. They also report averages over three runs without standard deviations or confidence intervals (please fix that one during the rebuttal)

**Anyway, those are technical details (although we could discuss the lack of a discussion section and a somewhat purely descriptive conclusion) what surprised me the most is the absence of an ethics discussion. The authors introduce TASWB, a new objective specifically designed to make backdoor attacks more effective, but don't discuss its potential misuse or broader implications. This is particularly striking given that the paper was submitted under an area related to “alignment, fairness, safety, privacy, and societal considerations”. I think that this alone could get this paper desk rejected at ARR but we’re not at ARR so please elaborate on that point.

Questions for authors
  • Why no ethical discussion, no discussion section, even at all ?
  • Why didn't you include the std deviation in all your 3-averaged results ?
  • Why did you only thoroughly test the easiest backdoor ? (the lexical one)

Comments on the paper

6 comments
AuthorsOpenReview ↗

Three-run variability

Three-run variability. Table 8 lists the default seed (42). Table 1 averages seeds 42, 43, and 44. For small-model AG News/BadNL, the ASRs are (99.63 ± 0.20)% for Mamba and (99.37 ± 0.57)% for Pythia. Both are near ceiling. Each cell below gives clean/triggered SD, computed as v1/2v^{1/2} (CACC/ASR in percentage points for classification, F1 on the [0,1][0,1] scale for SQuAD).

ModelDatasetBadNLSynBkdStyBkdBGMAttack
Mamba-130MIMDB1.57/1.661.82/23.561.50/1.951.41/7.87
Mamba-130MAG News0.37/0.200.46/1.350.00/0.510.30/0.76
Mamba-130MYelp1.41/0.360.85/2.310.91/4.641.26/4.55
Pythia-160MIMDB0.56/2.692.20/17.581.66/7.351.98/12.54
Pythia-160MAG News1.36/0.570.49/1.660.57/2.600.81/1.53
Pythia-160MYelp1.50/1.652.08/3.400.37/4.711.59/5.52
Mamba-2.8BIMDB0.51/1.040.30/0.460.40/5.200.20/1.56
Mamba-2.8BAG News0.37/0.000.10/0.100.17/6.240.17/3.11
Mamba-2.8BYelp0.75/0.460.26/0.501.10/1.550.69/1.52
Mamba-2.8BSQuAD0.010/0.0020.014/0.0320.023/0.1000.008/0.051
Pythia-2.8BIMDB0.10/0.650.56/0.320.50/1.630.75/2.75
Pythia-2.8BAG News0.61/0.000.35/0.000.47/1.230.35/3.21
Pythia-2.8BYelp0.51/0.371.01/0.350.26/2.141.27/0.98
Pythia-2.8BSQuAD0.005/0.0010.003/0.1050.025/0.0160.024/0.172
AuthorsOpenReview ↗

Response to Weakness 1 (Pythia baseline, learning rate, and statistics)

We sincerely thank the reviewer for this valuable comment. We agree that a shared learning rate can disadvantage one architecture and that small gaps need variances. We ran a new per-architecture tuning study and revised our claims accordingly.

1. Seeds and variance. All Table 1 entries are means over three independent fine-tuning runs (seeds 42/43/44). The "seed 42" in Table 8 is the default seed of the mechanism analyses, and we apologize for the confusion. We have reported mean ± std for every entry. For the example raised, AG News/BadNL ASR is 99.6±0.299.6\pm0.2 (Mamba-130M) vs. 99.4±0.699.4\pm0.6 (Pythia-160M). This gap is within seed variability, and we will no longer interpret it.

2. Per-architecture learning-rate tuning. We tuned Mamba-130M and Pythia-160M on IMDB and Yelp under BadNL (5% poisoning, 10k samples, same LoRA setup). Both models searched the same grid 5e-6,1e-5,2e-5,5e-5,1e-4,2e-4\\{5\text{e-}6,1\text{e-}5,2\text{e-}5,5\text{e-}5,1\text{e-}4,2\text{e-}4\\} (seed 40). The top-2 candidates plus 2e-5 were re-screened on seed 41. As Pythia's best value lay at the grid edge, both models were also tested at 5e-4. Selection used only a held-out validation split (CACC, then clean NLL), never test data or ASR. The selected LR is 2e-5 for Mamba on both datasets (our original setting) and 2e-4 for Pythia. At 5e-4 Pythia was worse and unstable, so its optimum lies inside the searched range. We then trained three fresh confirmation seeds (42/43/44) for 10 epochs and evaluated the 5- and 10-epoch checkpoints.

DatasetModel (LR, epochs)CACCASRTrigger-specific gain
IMDBMamba (2e-5, 5)91.4±0.264.4±0.248.2±6.6
IMDBPythia (2e-5, 5)80.2±0.873.6±1.420.8±9.3
IMDBPythia (2e-4, 10)84.8±1.368.8±4.548.4±6.4
YelpMamba (2e-5, 5)59.9±0.282.2±0.868.5±3.8
YelpPythia (2e-5, 5)46.6±0.983.6±1.817.6±12.9
YelpPythia (2e-4, 10)51.4±0.882.9±0.968.3±6.2

Mean ± sample std over 3 seeds. Trigger-specific gain = ASR − target rate when a matched control token (bb) is inserted at the same position.

  • The baseline was indeed under-tuned. With its own LR and 10 epochs, Pythia gains +4.5/+4.8 pp CACC. Mamba does not benefit from more epochs (−0.3/−0.4 pp).
  • The clean-utility advantage remains. We compare each model's best configuration, which gives Pythia twice the training budget. Mamba still leads by 6.6±1.56.6\pm1.5 pp (IMDB) and 8.5±0.98.5\pm0.9 pp (Yelp; 11.2/13.2 pp before tuning), and the gap is positive in every seed.
  • Backdoor susceptibility is comparable after tuning. At the shared LR, Pythia's higher ASR partly reflected generic target drift: the control token alone yields 52.7%/66.1% target predictions, vs. 16.3%/13.8% for Mamba. After tuning this drops to 20.5%/14.6%, and the trigger-specific gains become nearly identical (48.4 vs. 48.2; 68.3 vs. 68.5). On test inputs that both models classify correctly, their ASRs differ by ≤0.2 pp under the shared-LR and 10-epoch settings.

3. Relation to Table 1. For leak-free and fair LR selection, the new study uses a stricter protocol fixed before training. The setup therefore differs slightly from Table 1:

  • a 2,000-sample validation split held out from the training partition;
  • FP32 master weights with bf16 autocast;
  • one fixed optimizer schedule for both models (AdamW, constant LR, no warmup).

These changes raise CACC for both models: at LR 2e-5 on IMDB, Mamba goes from 85.2 to 91.4 and Pythia from 75.3 to 80.2, while ASR stays in the same range. Absolute numbers are thus not directly comparable with Table 1, but the conclusions agree: Mamba-130M has higher CACC than Pythia-160M in every setting, and the two models' BadNL ASRs are close. To keep the two protocols separate, we will keep Table 1 (adding std) and report this study in a separate appendix table. It will include the full protocol, per-seed values and the complete LR sweep.

4. Revised claims. We will:

  1. replace "a more favorable balance between clean performance and resistance to backdoor activation" with: at the 130M/160M scale, Mamba retains a clean-utility advantage after per-architecture tuning, while its susceptibility to BadNL is comparable to Pythia's;
  2. state that the 2.8B comparison uses shared hyperparameters, and present its ASR differences as observations under that protocol rather than as architectural conclusions;
  3. use the loss curves only descriptively;
  4. state that the tuning study covers BadNL on two datasets.

We thank the reviewer again for helping us make these conclusions more rigorous.

AuthorsOpenReview ↗

Response to Weakness 2 (component replacement, layers, head triggers, Pythia)

We thank the reviewer and have run the suggested layer-wise, downstream, head-trigger interventions.

1. Layers and the "by construction" concern. Table 6/17 replaces each component jointly in all 24 layers at the appended trigger/readout token. Recovery thus cannot be separated from readout editing. We will clarify this and present Table 6/17 as a readout-level intervention, not pathway localization.

2. New layer-wise interventions downstream of a head trigger. We use the BadNL head-trigger model (Mamba-130M, AG News, 5% poisoning, standard CE, no TASWB). On 281 held-out non-target texts, cf gives 100% ASR, while the matched controls bb/dd/cc give 10.0%/5.7%/7.1% target predictions. Inputs differ only in the head token. At a body position t=τ+kt=\tau+k, k∈8,32,64k\in\\{8,32,64\\}, we replace one component in one layer with its value from a matched input, then let the scan and all upper layers run normally. We test seven components, hth_t, gtg_t, rtr_t, mtm_t, wtw_t, Δt\Delta_t and the recurrent state sts_t. Each run modifies one component at one layer and position. We use three sweeps: (i) position: layers 18/19/20 separately at each of k∈8,32,64k\in\\{8,32,64\\} with full replacement (λ=1\lambda=1); (ii) layer: all 24 layers individually at k=32k=32 with λ=1\lambda=1; and (iii) strength: λ∈0,.25,.5,.75,1\lambda\in\\{0,.25,.5,.75,1\\} at fixed layer 19, separately for each of k∈8,32,64k\in\\{8,32,64\\}. Across seven components and three directions (control→cf, cf→control, control→control), this gives 2,646 distinct conditions after deduplication. Specificity is Δm(ctrl→cf)−Δm(ctrl→ctrl′)\Delta m(\text{ctrl}\to\texttt{cf})-\Delta m(\text{ctrl}\to\text{ctrl}') (paired bootstrap CIs).

L19, k=32k{=}32, λ=1\lambda{=}1Spec.ASRTrue-label acc.BrokenReverse
ht,gt,rt,mt,wt,Δth_t,g_t,r_t,m_t,w_t,\Delta_t≤0.001\le0.001100%0.0%0.0%7.6%
sts_t6.56 [6.26, 6.87]55.3%43.3%1.4%84.3%

Before intervention, ASR is 100% and true-label accuracy is 0%. Reverse means the cf donor injected into trigger-free control inputs (baseline 7.6%).

  • No recovery by construction. All replacements happen at the same non-readout position. Yet the six local components leave ASR at 100% in every tested layer, position and strength, with specificity ≤0.03\le0.03 and reverse rate ≤7.9\le7.9\\%. Only sts_t changes the output (paired difference about −6.56-6.56, CI [−6.87,−6.26][-6.87,-6.26], for each component).
  • Recovery, not breakage. The ASR drop under sts_t turns mainly into true-label recovery, with only 1.4% Broken.
  • Downstream propagation. The effect holds at k=8/32/64k=8/32/64 (ASR 53.3/55.3/61.7%, specificity 6.76/6.56/6.17). Injecting the triggered state raises the target rate of control inputs from 7.6% to 84.3%.
  • Layers. In the 24-layer scan, layer 19 stands out for sts_t (6.56; next largest 0.50). The scan is exploratory, so we will report all layers and not claim a unique layer.

These results indicate that the head-trigger signal propagates through the accumulated recurrent state, rather than being recomputed at each body token. Replacing a token's local components or its single write wtw_t cannot remove what the state already holds. This is the setting that motivates TASWB.

3. Pythia components. A Transformer comparison needs a comparably strong backdoor. Pythia's low head-trigger ASR creates a floor effect, as Fig. 2 shows under last-token readout. A new AG News run under one fixed protocol (BadNL head, 5%, same LoRA setup; 256 validation texts for CACC, 186 non-target texts for ASR) shows the same trend:

ModelEpochsCACCcf ASRMax controlGap
Mamba-130M591.0%98.9%6.5%92.5 pp
Pythia-160M1088.7%10.8%7.5%3.2 pp

Even with twice the epochs and comparable CACC, Pythia's ASR is only 3.2 pp above controls. This small trigger-specific gap limits component comparisons. We therefore omit Pythia interventions here, report this limitation, and do not claim the state pathway is Mamba-exclusive.

4. Revisions. We will:

  1. state the layer setting of Table 6/17;
  2. add the full head-trigger component analysis;
  3. replace "the mixer, gate, scan-output, and state-write pathways are the causal drivers" with "a causal contribution of the propagated recurrent state in the evaluated head-trigger setting";
  4. add the Pythia results and the floor-effect limitation.

We thank the reviewer for helping refine our mechanistic claims.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.