acceptodds
Under review as a conference paper at ICLR 2027

StegoBench: Evaluating steganography potential in language models through supervised learning

Abstract

Steganography is the act of hiding information in plain sight. Text-based steganography is an AI safety concern: hidden messages embedded in ordinary language model outputs would undermine their monitoring. This paper asks which known steganographic encoding algorithms from the wider literature can be trained as a model capability via supervised fine-tuning. We introduce StegoBench, a benchmark of 18 text steganography schemes spanning lexical substitution, syntactic transformation, structural encoding, and distributional generation. Across our full fine-tuning runs, SFT succeeds when encoding reduces to local token-level choices. The strongest evidence comes from lexical schemes: the Chang & Clark scheme reaches a hidden bit error rate (BER) as low as 0.011, and the Shirali scheme reaches a BER of 0.117–0.137. Schemes that require multi-token structural coordination or distributional control are far less reliable, and several generative schemes collapse during training. Model scale is not the main determinant of performance: small and mid-sized models often match larger models on trainable schemes. StegoBench provides a standardised testbed for comparing trainability, detectability, and failure modes across steganographic mechanisms.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
LLM steganography, AI Safety, benchmark

Reviews

Among:
Shape:
1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_VkGYOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2(+1)
Read review
Paper summary

This paper introduces StegoBench, a benchmark evaluating 18 text steganography schemes across diverse language models and training methods. Results indicate that supervised fine-tuning effectively learns local token-level encoding, whereas more complex schemes frequently collapse. Additionally, steganographic performance relies more on training data quality than model scale.

Critical strengths

This paper systematically evaluates 18 established text steganography schemes across diverse language models and training paradigms, offering key empirical insights into their trainability, detectability, and failure modes.

Critical weaknesses
  1. Method Coverage is not sufficiently up to date. The 18 selected schemes rely almost entirely on algorithms from 2023 or earlier, overlooking substantial methodological advances from 2024–2026. Although the paper cites several recent studies on LLM steganography, failing to evaluate these newer encoding methods in the benchmark is a critical omission.
  2. StegoBench’s unified SFT framework may introduce evaluation bias. Several modern steganographic methods rely on inference-time mechanisms, such as token distribution access, sampling control, or shared randomness. Forcing models to internalize these runtime processes through SFT likely misrepresents the original algorithms and explains their poor benchmark performance. Consequently, more rigorous and equitable comparison methods are needed for these approaches.
Questions for authors
  1. Could you provide more results from recent methods about linguistic steganography, especially those LLM-based steganography?
  2. Also, it is unconvincing to me that all these modern steganography method collapses and fails. Is there more strict analysis on the benchmark settings?
3 comments
AuthorsOpenReview ↗

Response to Reviewer VkGY

Q1

Since the original submission of this paper, we have studied TrojanStego (EMNLP 2025) and SparSamp (USENIX Security 2025).

  1. SparSamp is a distribution-coupled scheme in its design, and follows the same trend we have observed in other generative schemes. It collapses into very simple outputs and carries no capacity (raw BER 0.93-0.96 on Qwen2.5-3B, Gemma-3-4B, and GPT-OSS-20B).
  2. We trained TrojanStego on 25K samples on Qwen2.5-3B, GPT-OSS-20B, and Gemma-3-4B. We found that it fits into our Trainable tier with sBER from 0.012-0.087.

We will add both of these schemes to our final paper.

Q2

The benchmark measures one well-defined training method, supervised fine-tuning, and our conclusions are scoped to that training method. Other training methods may produce model organisms of modern generative distribution-coupled stego schemes. Under strict SFT, we have observed the same pattern across nearly all distribution-coupled stego schemes. Not every modern scheme fails. TrojanStego (2025), which encodes bits through vocabulary choices rather than by sampling from a model’s distribution, is Trainable under the same SFT setup. Distribution-coupled schemes rely on sampling directly from a model's distribution. As SFT pressure is applied to the model, that distribution shifts. This means that if you create a sample right before you use it with the model's current distribution, by the time the model has been trained on that sample, the underlying distribution has shifted in a way that would not produce that same sample. It is constantly chasing a moving target. Drift is not the full explanation of what is happening, however: removing it through self-distillation does not prevent collapse.

We have run numerous experiments to try and resolve this problem. None produced a working organism.

1. EOS/Special-token masking

Mask EOS and special tokens out of the loss, so the model can’t fall back on them. Instead of spamming special tokens, the model falls back to repeating extremely common English words.

2. Iterative self-distillation

Regenerate targets from the current checkpoint, and train on them over multiple rounds. The model still collapses into repetitive phrases and special tokens.

3. RL with the scheme’s decoder in the reward loop

Trained with REINFORCE, using a reward of 1 - BER from the scheme’s decoder plus a KL penalty. The output didn’t collapse, but the model wrote the secret as plaintext instead of encoding it.

4. Cross-checkpoint decoding

This was not a training experiment, but instead an analysis of the resulting artifacts. We used the same checkpoint for both encoding and decoding a message using the scheme’s implementation, and found that the payload could be recovered 75-100% of the time. We then did the same experiment using the base model and the training artifact, and found that it degrades to chance: BER 0.49-0.52 for Discop, Sallee, RNN-Stega and Moraldo. Wayner kept a weak signal (0.36-0.40).

Reviewer_VkGYOpenReview ↗

Response to Rebuttal from Reviewer VkGY

After reviewing the rebuttal, I am pleased to see additional recent work and have decided to raise my overall rating to 2. However, I remain unconvinced about using a benchmark on supervised steganography, which appears to have limited application.

I also noticed a strong indication of AI use in the revised paper, especially in Sections 4 and 5 (Results and Analysis). The content reads more like a data report and provides very little information. I suggest the authors and AC take this issue seriously.

AuthorsOpenReview ↗

Response to Reviewer VkGY on new revision

Thank you very much for your helpful feedback! During the course of editing the paper for the purpose of this rebuttal phase, we relied too much on AI assistance to incorporate updated results. This included using AI to identify all numerical values that needed to be updated, and then having it help update those sections. We have done another revision of the paper with this in mind.

Reviewer_LGtXOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

This paper presents StegoBench, a unified framework for evaluating the ability of language models to learn text steganography schemes through supervised fine-tuning. The benchmark covers 18 schemes and reports on message recovery rates, the detectability of steganographic text, and training failure phenomena.

Critical strengths
  1. The paper observes that some schemes, such as Chang–Clark et al., can be learned effectively by models, while several generative schemes that rely on probability distribution control exhibit output degradation after fine-tuning.
  2. The research addresses issues related to model security monitoring, and the benchmark development holds potential value.
Critical weaknesses
  1. Generative steganographic schemes involved rely on the token probability distribution of a specific language model to establish a bit-to-token mapping. This paper uses a frozen GPT-2-XL model to generate offline training samples, which are then used to fine-tune other models. Besides, I noticed the appendix also shows that message recovery degrades significantly when the encoder and decoder employ different checkpoints. Thus, the generation-based method exhibiting near-random BER or collapse into specific tokens may stem from the mapping varying with the model checkpoint, rather than necessarily indicating that the model is unable to learn the corresponding steganographic capability. I suggest further distinguishing between two types of failure: (a) the model has not learned the encoding mechanism and (b) mismatch between the encoder and decoder mappings.
  2. The number of training samples used by each scheme varies significantly. For example, Chang–Clark, Synonym, and Meral use approximately 5K, 20K, and 50K samples, respectively. In addition, the payload per sentence also ranges from 1 bit to 8 bits. Some approaches also utilized training data that had been filtered or combined across different capacities. Thus, the observed differences in BER may be influenced simultaneously by sample size, data quality, coding capacity, and algorithmic complexity, and do not necessarily reflect the trainability of the approaches themselves. It is recommended to conduct comparative experiments under standardized conditions regarding the number of training samples, payload capacity, and data quality, and to report capacity-sensitive metrics such as the number of correctly recovered bits per sentence.
Questions for authors
  1. Can a benchmark fairly compare the trainability of different steganographic schemes?
  2. Could the failure of a generative approach reflect a mismatch between the training objectives and the decoder, and can this be directly attributed to the difficulty of learning the approach?
2 comments
AuthorsOpenReview ↗

Response to Reviewer LGtX

Q1

Yes. StegoBench compares schemes through SFT, ICL, and ICRL with a consistent regimen per method. For SFT, a matched sweep at N = 20K (Qwen2.5-3B, same recipe, 4 seeds) shows that tier placement is stable across seeds (Shirali 0.064 ± 0.006, Meral 0.214 ± 0.011, Synonym 0.296 ± 0.010). We evaluate each scheme using its natural capacity on a given cover task, and report how payload and data size shift BER (see our response to Reviewer gZqT). We also report bits recovered per sentence alongside sBER, which reveals capacity differences that sBER does not. Across Qwen2.5-3B, Gemma-3-4B, and GPT-OSS-20B, Acrostics recovers 9.7-10.1 of 10.2 bits per sentence, Chang & Clark 2.4-2.8 of about 2.8, Shirali 1.18-1.20 of 1.23, Synonym 1.1-1.2 of 1.74, and Meral 0.87-0.91 of 1.30. Synonym recovers more bits per sentence than Meral despite a higher sBER, because each sentence carries more bits.

Q2

Our control experiments isolate the two failure modes the reviewer is describing. Cross-checkpoint decoding shows that mismatch between encoder and decoder substantially reduces recovery: matched checkpoints recover 75-100% of payloads, whereas mismatched checkpoints drop to near chance (BER 0.49-0.52) for DISCOP, Sallee, RNN-Stega, and Moraldo (Appendix H).

To test whether this mismatch alone explains the failure, we removed it by construction: in iterative self-distillation, training targets were regenerated from the current checkpoint each round, so the encoder and decoder were the same model rather than the GPT-2-XL reference used to generate the training data. Training still collapsed into repetitive phrases and special tokens (Qwen2.5-0.5B; Section 6).

We then removed the fixed targets entirely: training with REINFORCE using the scheme’s decoder in the reward (1 - BER plus a KL penalty) avoided collapse, but the model learned to write the secret as plaintext instead of encoding it (Section 6). Even when optimized directly against the decoder, the model did not learn the distribution-coupled encoding.

We therefore attribute the failures of a generative approach to the interaction between the tested training methods and distribution coupling rather than the schemes’ inherent difficulty alone. We will revise the paper to state this distinction and scope our claims to the training methods tested.

Thank you for the clarification. Your response addresses my concerns, and I will retain my original score.

Reviewer_gZqTOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

StegoBench studies whether language models can learn specified text steganography algorithms through supervised fine-tuning. It incorporates 18 schemes into a unified reference encoder and decoder framework, evaluates three main model families, and conducts Qwen scale experiments on some schemes. The paper also compared instruction based prompts and two iterative prompt methods.

Critical strengths
  1. This is a new idea that no one has paid attention to before.
  2. Use algorithm reference decoders to compare multiple explicitly specified steganographic schemes, distinguishing the ability to execute established encoding rules from the ability of neural receivers to guess messages.
  3. Some positive results of SFT have good support, and the paper also distinguishes between repeated output crashes and situations where text flows smoothly but encoding fails. These observations are valuable.
Critical weaknesses
  1. Since these steganographic schemes already have encoders that can be directly called, what additional capabilities or risks do we hope to uncover by studying language models training to execute these schemes on their own?
  2. Is the current supervised training setting suitable for testing the learnability of steganographic schemes that rely on token by token probability distributions or internal states? What is the controlling evidence that can distinguish the reasons for model failure to learn encoding, reference distribution mismatch, and unstable training process when training fails?
  3. The training conditions of different schemes are inconsistent, making it difficult to explain the results as differences in the learnability of the schemes themselves.
Questions for authors
  1. How sensitive are the four trainability categories to the data, payload size, and training configuration?
  2. Has the author distinguished the impact of model size, whether the training configuration is suitable for that size, and the impact of the optimal running choice? The existing results directly support the statement that 'under the current training formula, the large model does not have stable benefits'.
1 comment
AuthorsOpenReview ↗

Response to Reviewer gZqT

Motivation: learning an encoder in the model’s weights

An encoder a model calls is something that can be seen with basic monitors. Tool calls are logged, the encoder’s code can be inspected, and access can be shut down. The risk we are studying is a model that does not need that. A model that has stego capabilities in its weights and produces stegotext as ordinary output could be much more difficult to monitor. StegoBench measures which schemes a model can learn, and how detectable the output is when it does. This is not a hypothetical condition. TrojanStego (Meier et al., 2025) shows a model can be fine-tuned to leak secrets through its normal outputs. Our results show which schemes are trainable (local and text manipulation rules such as Shirali, Chang & Clark, Acrostics and TrojanStego), and which are not under SFT (distribution-coupled schemes, which collapse).

Sensitivity to data, payload and training configuration

We ran a set of controlled ablations using Qwen2.5-3B. Tier assignments are stable across multiple seeds (standard deviation ≤ 0.011). Changing the amount of training data has a large impact on trainability, and the ablations below show by how much. The budget used for each scheme is a trade-off between training cost and how far the scheme can be pushed. Payload can have a large effect (see below), but we use each scheme’s natural capacity so that the benchmark measures the schemes as designed.

Seed (4 seeds, fixed configuration)

  • Shirali: 0.064 ± 0.006 (0.0620, 0.0685, 0.0685, 0.0555)
  • Meral: 0.214 ± 0.011 (0.2274, 0.2005, 0.2110, 0.2157)
  • Synonym: 0.296 ± 0.010 (0.2960, 0.3062, 0.2980, 0.2828)

Learning Rate (1e-5 / 5e-5 / 1e-4, seed 0)

  • Shirali: 0.082 / 0.062 / 0.052
  • Meral: 0.216 / 0.227 / 0.208
  • Synonym: 0.478 / 0.296 / 0.225

Data size

  • Acrostics: Partially Trainable at 20K (0.135), and Trainable at 50K (0.044)
  • TrojanStego (LoRA): 0.472 at 50K, 0.202 at 250K, and 0.154 at 750K.
  • Atallah: Remains at chance from 5K to 50K

Payload

  • Synonym: 0.098 at 1-bit vs 0.296 at natural
  • Chang & Clark: 0.15 at 2-bit payload vs mixed 2/4/8-bit at 0.033
  • Meral: 0.046 at 1-bit vs 0.227 at natural

Model size and training recipe

Our scale sweep deliberately holds each scheme’s training recipe fixed, only scaling learning rate with each run’s global batch size, so it measures how a recipe developed on smaller models transfers to larger ones. We did not tune hyperparameters per scale, so we do not claim larger models cannot do better. Under this recipe, Shirali stays Trainable from 0.5B to 72B (sBER 0.021-0.096), though its error rises slightly above 3B. Our claims are scoped to this recipe, and we will make this explicit in the revision.

Reviewer_xTFpOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper introduces StegoBench to evaluate the ability of large language models to learn existing text steganography schemes through supervised fine-tuning. The authors collect 18 steganographic schemes and compare SFT, ICL, and ICRL across multiple language models. The results show that local lexical substitutions and certain syntactic transformations are easier to learn, while schemes involving complex structures or token probability distributions perform poorly, with some exhibiting generation collapse. The authors also investigate the effects of model scale, training data quality, and checkpoint changes on steganographic capabilities.

Critical strengths
  1. The paper brings together 18 text steganography schemes under a unified framework for encoding, decoding, and evaluation.
  2. The experiments cover multiple language models and different learning paradigms, including SFT, ICL, and ICRL, providing broad empirical coverage.
  3. The analysis of generation collapse, cross-checkpoint decoding mismatch, and training data quality reveals several interesting empirical findings.
Critical weaknesses
  1. The authors argue that local token-level decisions are easier to learn. However, Atallah, which involves syntactic transformations, achieves a BER of around 0.02, while Shirali, based on simple spelling substitutions, has a BER of 0.117–0.137. The schemes also differ in encoding rules, training data, and supervision targets. More targeted experiments are needed to identify the key factors affecting trainability.
  2. Training set sizes vary from 5K to 50K across schemes, and payload capacities also differ substantially, making direct comparisons difficult. Moreover, Chang & Clark achieves a best-run BER of 0.011 on Qwen-3B, while the mean across five seeds is 0.024. Reporting the best run rather than the mean may overestimate the model's performance.
  3. The authors only use a logistic regression classifier based on simple linguistic statistics, without evaluating stronger text steganalysis methods. In Table 1, Synonym achieves AUROC values of 0.235–0.273, substantially below 0.5, which may indicate discriminative information in the reverse direction. The current experiments provide insufficient evidence to support the paper's conclusions about steganographic detectability.
  4. In Figure 2, SFT uses a 4-bit payload for Meral, whereas RSQ is actually evaluated with a 1-bit payload, making the direct comparison unfair. The paper also relies heavily on heatmaps, some of which have crowded labels and poor readability. Important observations, such as performance degradation with increasing model scale, improvements from data quality, and generation collapse, lack deeper analysis.
Questions for authors
  1. How do the authors explain the difference in trainability between Atallah and Shirali? Can controlled experiments disentangle the effects of encoding rules, data quality, and supervision targets? Is the failure of generative steganography mainly caused by the mismatch between the reference encoding distribution and the SFT model distribution?
  2. How do the authors ensure comparability when different schemes use different training set sizes and payload capacities? How is BER calculated for samples where the full payload cannot be embedded? Why does the main results table report the best runs rather than the mean and standard deviation across multiple random seeds?
  3. How do the authors explain the AUROC values substantially below 0.5 for Synonym? Has the direction of the detection scores been checked? Would the current detectability conclusions still hold when stronger text steganalysis detectors are used?
  4. Given the different payload sizes across learning paradigms in Figure 2, can the authors provide comparisons under matched settings? In addition, can the authors further investigate the causes of performance degradation in larger models and generation collapse, rather than simply reporting the experimental results?
1 comment
AuthorsOpenReview ↗

Response to Reviewer xTFp

Q1

Since submission, we found and corrected an error that directly affects this comparison. For Atallah, sBER was calculated incorrectly for this scheme, and our implementation did not use the original keyed bit definition. With both of these corrected, Atallah is at chance on every model we trained (sBER 0.38-0.44), and moves from Trainable to Not Trainable. For Shirali, further training runs with that scheme since submission have shown that it is in fact Trainable (sBER 0.021-0.096). The corrected results more strongly support the paper’s conclusion: Shirali’s encoding is a simple spelling choice, while Atallah depends on a keyed hash the model would have to compute.

Controlled experiments can isolate these factors. In a matched sweep, we kept the model, training recipe, data size, and seeds fixed (Qwen2.5-3B, full fine-tuning, N = 20K, 4 seeds) and varied only the scheme. The results match the paper’s tiers: Shirali 0.064 ± 0.006, Meral 0.214 ± 0.011, Synonym 0.296 ± 0.010. Data quality is held constant, because every training target is round-trip verified at 0 BER with the reference decoder. We have further data-size and payload ablations in our response to Reviewer gZqT.

Distribution drift is a significant cause of collapse, but not the only one. Decoding with a different checkpoint than the one that encoded drops recovery to chance (BER 0.49-0.52). This shows that mismatch alone can break a scheme, but removing the mismatch does not prevent collapse. We have experimented with frozen reference models, sampling directly from the model in training, and iterative self-distillation, where targets are regenerated from the current checkpoint each round. None of these experiments led to a model that does not collapse. When we instead experimented with RL, optimizing directly against the scheme’s decoder, the model avoided collapse, but wrote the secret in plaintext instead of encoding it.

Q2

Schemes have a natural capacity based on the cover task. In any given cover task there are only so many possible substitutions that can hold capacity. To account for this, we unify our sBER calculation across all schemes. sBER is the fraction of attempted bits, pooled over the whole evaluation, that are not recovered correctly. Pooled BER is folded once at 0.5. Cells whose pooled raw BER over 0.85 are treated as failures (shown as -), the same rule as our ICL/ICRL appendix. Missing bits count as errors: payloads are sized to the cover’s natural capacity, so a reference decode always recovers the full payload.

We report a single run per cell, partially due to cost. For Chang & Clark on Qwen2.5-3B, the five-seed mean (0.024) is well below the 0.10 Trainable cutoff. We have run seed sweeps on individual combinations, and the standard deviation is very small (per-seed values in our response to Reviewer gZqT).

Q3

The score direction is correct. Sub-0.5 values were caused by how our cross-validation split the data. Each stegotext and its baseline paraphrase the same source sentence. With Synonym, this often yields nearly identical samples, so our probe was scored on a near copy of the training example with an opposite label. We confirmed this by running a control experiment where labels were swapped randomly within pairs, eliminating the real signal. That procedure yields AUROC 0.16-0.20, whereas folds grouped by source text yield 0.49-0.52. With grouped folds, Synonym’s AUROC is 0.53-0.59, near chance and consistent with our paper’s conclusions. Table 1 and the detectability appendix now use grouped cross-validation.

Stronger detectors support the same conclusion. Using TF-IDF logistic regression, gradient boosting, and a fine-tuned RoBERTa classifier, stegotext remains hard to distinguish from the same model’s non-stego outputs (AUROC 0.50-0.64 for Shirali and Synonym; Qwen2.5-3B). Synonym retains a modest signal (up to 0.64), and Shirali remains near-undetectable (≤ 0.56).

Q4

We re-evaluated RSQ on Meral at 4 bits. The original Figure 2 cell used a 1-bit payload. At 4 bits, RSQ stays at the level of the unchanged-cover baseline across all six models (median raw BER 0.475 vs 0.45 for chance). The matched setting now preserves the paper’s ordering with SFT ahead of ICRL. We have updated Figure 2 accordingly and improved the readability of heatmap labels while regenerating them.

For larger model degradation, we held each scheme’s recipe fixed across model size, with the learning rate scaled to each run’s global batch size. A direct test suggests the recipe, not model size, drives part of the degradation: holding Qwen2.5-14B fixed and changing only the global batch size from 512 to 128 gives four times as many optimizer steps, and halves sBER for Shirali from 0.131 to 0.065. Per-scale hyperparameter sweeps are beyond our scope, so we scope our claims to this recipe (see our response to Reviewer gZqT).

For generation collapse, see our answer to Q1 and our response to Reviewer LGtX.

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

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