What's Producible May Not Be Reachable: Measuring the Steerability of Generative Models

Thank you for your insightful review. Your comments were very constructive and have improved the paper. To summarize the main changes, we've added:

• Analysis for different numbers of allowed rewrite attempts
• Further comparison of CLIP/Dreamsim to human metrics
• Clarification about experimental design

You cap each reproduction attempt at five prompts and forbid negative prompts or ControlNet style constraints. Why were those particular limits chosen, and how sensitive is the failure rate to relaxing them? A small ablation that doubles or halves the attempt budget, or that enables commonly used guidance knobs, would establish whether the headline 60 percent unsatisfied rate is intrinsic or policy driven.

It's a good idea to look at how sensitive results are to the number of attempts. We've added results below across different numbers of prompts, which we'll add to the paper:

For all of the number of rounds, unsatisfactory rates are within 4% of the headline result (60% dissatisfaction). The paper considered five attempts because we found only marginal improvement after the third attempt. We also feel that five is a realistic number of times a user would try rewriting prompts. We completely agree that longer time horizons (e.g. multiple days of weeks) would be interesting, and we don't mean to suggest that people cannot improve over time. We'll emphasize these points in our revision.

We focused on features that were shared across APIs, which is why we didn't include negative prompts or ControlNet style constraints. We did try an experiment (Table 6 in the appendix) where we allowed users to specify classifier-free guidance (CFG) settings in addition to text prompting. We could only test Stable Diffusion models for this because not all APIs had CFG. Users didn't show significant improvement with or without CFG (DreamSim similarity score, higher is better, SE in parentheses):

We think testing more advanced features would be interesting. These mechanisms are all amenable to the framework in the paper, and we hope that future work will study additional features.

The predictor uses CLIP embeddings, yet CLIP correlates only 0.32 with human judgments, so relying on it to partition gains risks substantial error propagation.

Thanks for bringing this up. We wanted to clarify a potential confusion: the 0.32 CLIP correlation shows that the CLIP score between a user's prompt and the resulting image has a low correlation with the steerability score for that image. This suggests that CLIP scores can be high with poor steerability, e.g. if many images are consistent with a single prompt or if a user has many desiderata that are infeasible to convey in a single prompt. Meanwhile, the predictor in the decomposition in Section 4 uses CLIP not as a score but as an embedding to a larger model and uses it not for the user's reproduced image but for the goal image (the goal is to predict how steerable a given goal image is, so it's not a function of reproduced images). We find that these models achieve an R^2 of almost 0.50, explaining almost half of the variance in poor steerability. We realize the writing wasn't as clear as it should've been, and we'll update this in the main paper.

When we use CLIP elsewhere in the paper, it's to compare its scores to human scores. We agree that it would be risky to rely on CLIP as a proxy for humans without benchmarking, so we use human annotations for our main experiments in Section 3. We've also included analysis below (which expands on results in the appendix) to compare human-based annotations to automated ones (based on CLIP and DreamSim scores), which finds that the automated annotations have high correlation with the human-based ones:

The claim that image steering "more than doubles" improvement is true on DreamSim deltas, yet the baseline improvement is itself tiny, so the practical effect size is unclear.

We agree that the baseline improvements look small in DreamSim score, and that DreamSim units can be hard to interpret. For a more interpretable metric, note that the improvement rate for text steering is ~55% compared to ~72% for image steering. This is an improvement from 5% over chance to 22% over chance, which we feel is sizable.

The LLM study forbids any lexical overlap with the target text. That constraint is not typical of real usage, where reusing phrases is often encouraged to preserve semantics. Could you report satisfaction scores when overlaps are allowed, or justify why the overlap prohibition models an important practical scenario?

Our goal with the LLM experiments is to capture one frequent use-case for LLMs in writing: to rewrite a passage for a user who can identify the style they want when they see it, but is unable to articulate what exactly that style is. For example, a student wishing to use an LLM to edit academic, technical writing may not get what they're looking for if they prompt an LLM to provide edits that match "academic, technical writing". However, even if they don't know exactly how to describe the writing they want, they are usually able to identify the examples they're happy or unhappy with when they see them. Our results found that this aspect of steerability is difficult for LLMs. We think this results adds to the conversation about LLM steerability: like you suggested, there are many uses where LLMs might be steerable (e.g. solving math problems), but in this focused aspect of writing to match a certain tone, they are less steerable. However, we don't aim to suggest that writing/editing is the only use-case for LLMs, and we will rewrite that section to emphasize these points.

The blind-LLM baseline achieves 52% of human improvement with no goal awareness, implying that the benchmark rewards prompt lottery effects rather than systematic steering.

This is a great point. The purpose of the blind LLM is to serve as a baseline. We want to clarify that the blind LLM does not do well, and it helps calibrate human improvement, which is already small. This could be seen as analogous to image classification experiments, where an image classifier that always predicts the majority class is included to show how well an uninformative model can perform. We feel the LLM is a useful baseline, but another option is to limit the number of human attempts to 1, so there is no lottery effect. This is an important point and we'll add it to our discussion.

The authors collected 18 k human ratings but provide no analysis of demographic effects.

While the data we recorded does not include demographics, we also recruited professional prompt engineers to perform the benchmark task via Upwork and compared them to the nonprofessional group. We found that professionals were better than the average steerer from the nonprofessional survey, but only slightly: final similarity scores were only 10% higher than for nonprofessionals. Moreover, we find that professional prompt engineers don't reliably improve between their first and last attempts, with even lower improvement rates than among the nonprofessional cohort.

That said, the decomposition is mathematically straightforward once the goal is stated, and the benchmark design (i.e., reproduce the model's own sample) is a narrow proxy for real user intent.

We completely agree that the decomposition is mathematically straightforward. We feel this simplicity is a strength: a simple decomposition is easier to interpret than a more complicated formula. You're also correct that the goal image is sampled from the same model used for steering. As discussed in Section 2, this ensures that steerability is independent of producibility: if a user can't reproduce the goal image, it's not about the quality of the model's images, just its steerability.

Asking workers to replicate potentially copyrighted output raises legal issues. Improving steerability may also facilitate malicious uses; this is acknowledged only briefly.

Thanks for raising this concern. We designed the benchmark with the goal of avoiding copyright issues: each image used in the benchmark is generated by a text-to-image model, and is not drawn from any external, copyrighted dataset. Still, as with any use of text-to-image models, it's possible that a model may produce a copyrighted image, and we will bring this up in our discussion. On the broader question of potential misuse, we agree that improved steerability could be dual use. That said, we believe that understanding and quantifying steerability is an important prerequisite for responsible deployment and mitigation planning. We'll expand on these points in our revision.

Thank you for your positive review of our paper. We're glad that you found the framework novel and valuable, and the experiments to be comprehensive and "likely to inspire further research in this direction."

We respond to your comments below. We hope our comments have addressed your questions. If not, please let us know if you have any more questions we can address in the follow-up.

The use of CLIP similarity and DreamSim captures high-level alignment but may overlook fine-grained fidelity. Since steerability often depends on whether specific details (e.g., exact number of objects, spatial arrangements) can be reproduced, would the authors consider incorporating or comparing against MLLM-based evaluators (e.g., GPT-4o, Qwen2.5-VL) that could better judge localized attribute matching? Evidence that CLIP-based metrics align well with human or MLLM-based fine-grained evaluation would strengthen the current claims.

It's a good idea to compare automated alignment metrics with those of humans. We've included analysis below comparing human-based annotations to automated ones (based on CLIP and DreamSim scores), which finds that the automated annotations have high correlation with the human-based ones:

Correlations with human ratings are high for both DreamSim and CLIP. Based on your suggestion, we also considered using GPT-4o as an MLLM-based evaluator. Because of API costs, we collected similarity scores from GPT-4o using a sample of 500 responses. The average scores for the human ratings and GPT-4o ratings on this sample are below:

So the MLLM-based evaluation also has a strong correlation with the human ratings, but not as strong as CLIP or DreamSim.

Given that the T2I benchmark requires users to prompt a model based on a target image, how do the authors account for the high variance caused by differing levels of user familiarity with prompt engineering or specific model behaviors? Could the authors report or control for user background (e.g., prior experience with prompting or specific models)?

Great suggestion. While the crowdsourcing platform we use does not allow us to filter by prompting expertise, we also recruited professional prompt engineers to perform the benchmark task via Upwork and compared them to the nonprofessional group. We found that professionals were better than the average steerer from the nonprofessional survey, but only slightly: final similarity scores were only 10% higher than for nonprofessionals. Moreover, we find that professional prompt engineers don't reliably improve between their first and last attempts, with even lower improvement rates than among the nonprofessional cohort. We think the comparison between these two groups is quite interesting, and will emphasize it in the revised paper.

Many modern T2I workflows involve multi-round editing or prompt refinement (e.g., iterative inpainting or variation selection). Why does the benchmark focus only on one-shot or limited prompt-based steering?

It's a good idea to consider multi-round editing or inpainting. However we faced a practical challenge: most of the models were only available via their APIs. Because our goal was to compare models, we focused on features that were shared across APIs, which is why we didn't include multi-turn interactions. There are many possible steering mechanisms and we don't mean to suggest that our paper considers all of them; only the common ones that are shared across APIs. We will clarify this in the paper.

To understand whether users were struggling to steer because of lack of control to more advanced features, Table 6 in the Appendix includes an experiment where we allowed users to specify classifier-free guidance (CFG) settings in addition to text prompting. We could only test Stable Diffusion models for this because not all APIs had CFG. Users show no significant improvement with or without CFG (DreamSim similarity score, higher is better, SE in parentheses):

One broader question is whether LLMs should be evaluated for steerability in the same way as T2I models... The authors could clarify what specific failure modes or gaps in LLM usability motivated their inclusion in this study, and what new insights this part of the benchmark contributes beyond prior understanding.

Our goal with the LLM experiments is to capture one frequent use-case for LLMs in writing: to rewrite a passage for a user who can identify the style they want when they see it, but is unable to articulate what exactly that style is. For example, a student wishing to use an LLM to edit academic, technical writing may not get what they're looking for if they prompt an LLM to provide edits that match "academic, technical writing". However, even if they don't know exactly how to describe the writing they want, they are usually able to identify the examples they're happy or unhappy with. Our results found that this aspect of steerability is difficult for LLMs. We think this results adds to the conversation about LLM steerability: like you suggested, there are many uses where LLMs might be steerable (e.g. solving math problems), but in this focused aspect of writing to match a certain tone, they are less steerable. However, we don't aim to suggest that writing/editing is the only use-case for LLMs, and we will rewrite that section to emphasize these points.

Thank you for your positive review of our paper. We're glad that you appreciated the ideas, methods, and experiments described in the paper. We respond to your comments below; to summarize the main changes, we've added:

• New analysis that includes comparisons with different success metrics
• Analysis of time taken as a possible cause of poor steering
• Clarification about experimental design

We hope our comments have addressed your questions. If not, please let us know if you have any more questions we can address in the follow-up.

Here is a key reference that is missing [1]. It shows that text-to-image models based on CLIP encoder (which is the case for at least Stable Diffusion, I have not checked for the other models used in the paper) share "systematic failures"... Studying the potential causes of poor steerability would have improved the benchmark... For instance, it would have been useful to inform the humans about the "systemic failures" of generative models beforehand, to improve the effect of the prompt rewrites.

Thank you for providing the reference -- we will add it to the paper. We think it brings up an important and relevant point: one factor of poor steerability is that CLIP's representations share systematic failures. It's tough to fully determine how much CLIP factors into the failures we see because most models have not released details about whether they use CLIP, but we will add a discussion of this point to our main results.

We find that another important factor is that prompt-image alignment metrics (like CLIP) between a user's prompt and their reproduced photo is not very predictive of steerability: the correlation between CLIP and steerability scores is only 0.32. This suggests that intent is not well-captured by prompt-image alignment metrics, e.g. if many images are consistent with a single prompt or if a user has many desiderata that are infeasible to convey in a single prompt.

We've also performed more analysis focusing on the role of time: we measured effort levels by measuring how long different kinds of steering (image vs text) take. We find that not only is image steering more effective, but it's also faster than text prompting (14 minute vs 10 minute median length). This suggests one cause of poor steerability: writing careful text prompts is time-consuming, and people might get tired:

Informing humans of the systemic failures of T2I models is an interesting idea. We recruited professional prompt engineers -- who all had experience with T2I models and their failures -- to perform the benchmark task via Upwork. We found that professionals were only slightly better than non-professionals: final similarity scores were only 10% higher than for nonprofessionals. Moreover, we find that professional prompt engineers don't reliably improve between their first and last attempts, with even lower improvement rates than among the nonprofessional cohort. This suggests that just being aware of the failures of T2I models doesn't result in significant improvement.

We will add these analyses and more to the discussion in our paper.

Because the goal is too hard, humans fail to accomplish the goal, no matter the model used (cf. Figure 2: similarities are quite low (mostly below 5 out of 10)). To me, they should not be compared to "Perfect similarity" but a different reference value.

You make a great point: users struggle to steer when they use text as a mechanism. This motivated us to look at other mechanisms, and we found that although no mechanism results in perfect performance, improvement is possible -- for example, image steering (especially with RL) shows improvement.

Additionally, the blind LLM in Figure 3 provides one kind of baseline: a steering mechanism that corresponds to randomly rewriting prompts without access to the goal image. The fact that this baseline achieves half of the human improvement helps calibrate the human performance against a baseline.

Still, we don't expect users to exactly create their goal image, so we've also performed a new experiment that simulates users being equally happy with multiple goal images instead of one. Specifically, instead of measuring performance by distance to the goal image, we say that a steerer has succeeded if they produce any image within some distance. The table below shows the success rate for different thresholds:

To get more than 50% success, the threshold needs to be 0.666 DreamSim score or lower. Empirically we find pairs of images at this threshold are not very similar. Steering remains challenging even with this relaxed definition of success.

Can you clarify how the prompt rewrites are made? Is this as part of a conversation or is it always from scratch?

This is a good point, and our paper should have been more clear: Prompt rewrites are always from scratch. That is, a user sees their previous prompt, they're given the opportunity to edit it, and then submit it to the model. We completely agree that doing a conversation might pose a problem, which is why we have each prompt attempt made independently, for both text and image generation. We'll clarify this in the revision.

Could you clarify the random image steering? Is it that you propose variations of the images with random perturbations in latent space, then the human chooses the best, you generate again variation of this chosen image, and repeat for several rounds?

Yes this is exactly right. Importantly, we choose the same number of rounds as in text steering so that the results are comparable. We provide more details in C.2 but we'll make this more clear and move it to the main text in the revision.

Note: there is an hyperlink issue line 673.

Good catch. This should read "Figure 3". We'll fix it in the revision.

Thank you for your positive review. We're glad you found the paper insightful and empirically valuable. We respond to your comments below; to summarize the main changes, we've added:

• An experiment where users try to steer images toward stock images, and we find that the steering scores are indeed worse than in the original survey
• More analysis of how similar the human ratings are to the automated ones

However, the metric being heavily human-dependent, and thus expensive to compute or improve on. More work can be put into automating parts of the assessment and proving the automation does not hurt precision.

This is a great suggestion. The main metrics in the paper rely on humans as annotators and steerers. While we use humans because measuring steerability involves measuring people, as you point out, this makes the metrics harder to automate. We've included analysis below, which expands on the analysis in the appendix to compare human-based annotations to automated ones (based on CLIP and DreamSim scores). We find that the automated annotations have high correlation with the human-based ones:

We also tried comparing human ratings to MLLM-based ratings like GPT-4o, which also found high correlation (0.67), although not as high as for DreamSim or CLIP (see response to hQSC).

Replacing human steerers with automated methods is trickier, because there is less evidence that large multimodal models can capture human behavior with high fidelity. Still, in our image steering experiments, we use a simulated human as part of an RL method to learn the images to suggest to people. While our results show that the simulated human is accurate enough to result in improvement over a baseline, we think more work is needed in order to assess whether automated steering can be a good proxy metric for human steering.

While I understand the theoretic need for separating producibility from steerability, I wonder, if we repeated the same experiment with any type of goal image (e.g., a collection of stock photos), would we see the same metric values, or would we see lower satisfcation numbers because the images are not reproducible? I think this is an important comparison that would add to the paper's claims.

This is a great suggestion. Based on your suggestion, we ran an experiment during the rebuttal period where the goal images were randomly sampled stock images (so they weren't necessarily producible by the model), and users were prompted to steer DALL-E 3 toward them. Across 130 attempts, we found that the similarity scores (based on CLIP) were indeed uniformly smaller than the model's scores in the main survey (when the goal image was sampled from the model's producible set):

For reference, every model's CLIP score in the main survey was in the range of 0.75 - 0.85, so the stock image setting would be worse than any of the 10 models in the survey. We agree this comparison is important, and we believe it will strengthen the paper.

I also found the LLM assessment to be somewhat lacking. LLMs are rarely used in this scenario of reproducing a text in exactly the same way, but rather to generate text in a broader context... I think the metric does not fit the LLM scenario and this part should not have been included in the paper.

We completely agree that our metrics are a more natural fit for the image models than LLMs, which is why we focus on image models. Our goal with the LLM experiment is to capture how LLMs are often used in writing: to rewrite a passage so it looks a certain way but without being able to verbalize what exactly the final text should be. We agree with your suggestion: we'll move the LLM experiments to the appendix, and spend more of the main text focusing on analysis.

I commend you for adding standard errors in tables, please be more consistent in labeling them in the captions of all tables.

Thank you. We will add more labels in the captions of the tables to point to the standard errors.