WorksComputer Science
Measuring the collaboration, not the agent
Abstract
Benchmarks for visualization agents score the agent alone; the human only supplies reference answers. For high-dimensional data this misses what matters: the knowledge of which variables count is held by on-site experts, not by the model, so the useful question is how well an analyst and an agent do together. We study one specific form of collaboration, the agent proposes a view, the analyst accepts, rejects, or modifies it, and those judgments are kept for later sessions, and propose five measures for it: complementarity, intervention efficiency, appropriate reliance, knowledge retention, and agency. The first four are computed from interaction logs alone. We test the measures, not people: in a testbed for parallel-coordinates design on public manufacturing data (UCI SECOM), with a simulated analyst whose behavior we control, all four are computable and respond to the controlled differences. Whether they reveal anything about real analysts is the next step; we release the testbed for it.
Introduction
In brief. When an analyst and an AI agent design a visualization together, how do we tell whether the pairing helped? We propose four log-based measures and one survey-based measure of the pair, and show on a simulated analyst that the four log-based ones can be computed and that they move when the collaboration changes. We do not show what they reveal about real people.
Benchmarks measure the agent. Large multimodal models now produce valid and often reasonable charts from natural-language requests, and an evaluation infrastructure has grown around them quickly—VisEval for NL-to-visualization validity [5], nvBench 2.0 for ambiguity resolution [13], VisJudge-Bench for visualization quality judging [24], DV-World for realistic multi-step scenarios [16], and SciVisAgentBench for scientific visualization agents [3]. All of these, however, measure the AI in isolation: the human supplies reference answers or labels, or is replaced by a user simulator [16]. Collaborative systems exist [1, 20], but building one and showing that the collaboration is what helps are different problems, and for the latter visualization has no yardstick.
Why high-dimensional data needs one. For a scientific volume, a good view is largely fixed by the data’s own geometry, and the knowledge needed to find it is general enough to be in a pretrained model. For high-dimensional abstract data—hundreds of anonymous sensor channels, say—neither holds. Choosing which few of hundreds of variables to show, in what order, is a combinatorial choice with no geometric anchor; whether a view is good depends on the question asked; and the knowledge of which sensors matter for this plant lives with its engineers [11], not in any model. The agent can search the space and the expert can judge it; each holds part of what is needed, so performance is a property of the pair. And because that expert knowledge is missing from the model, the agent should keep what it is told rather than be retaught every session, which raises a question agent-only benchmarks never ask: does the agent need less correction over time? Collaboration also cannot be assumed to help—AI suggestions can fixate designers and narrow exploration [22, 17]—so it has to be measured.
Which collaboration. We study one deliberately narrow form: the agent proposes a view, the analyst accepts, rejects, or modifies it, and the analyst’s judgments are kept and fed back to the agent in later sessions. This is persisted corrective feedback, not open-ended co-creation or joint brainstorming; we use “collaboration” in this sense throughout.
Contributions. (1) An argument for measuring the analyst–agent pair in high-dimensional data (§3). (2) Five measures (“axes”) of the pair; four are computed from interaction logs (§4). (3) A testbed showing those four are computable and respond to controlled variation (§§5–6)—validation as instruments, with a simulated analyst, not a claim about people. (4) The testbed and log format, released for human studies.
Background
Visualization agents and collaborative systems. Beyond the benchmarks above, evaluation-centric work taxonomizes scientific visualization agents [2]; none measures the human–agent team. Collaborative systems such as HiLSVA [1] and BONSai [20] build on paired recommendation, proactive intervention, and multimodal intent [23, 25, 4], descending from semantic interaction [6]. Recent work organizes agentic visual analytics into roles and workflows [14] and finds persistent agent memory helps only insofar as retained feedback is of high quality [21]—foreshadowing our retention axis.
Collaboration measurement elsewhere. Human–AI teaming constructs visualization has not imported: complementarity, requiring team loss strictly below both solo losses [9]; appropriate reliance, separating justified from blind acceptance [18, 8]; readiness, whose learning-over-time family is to our knowledge the only existing construct for longitudinal knowledge transfer in a team [10]; and frameworks for selecting metrics by collaboration mode [7]. Outside visualization, team-level benchmarks have begun to appear: CentaurEval builds coding tasks that neither humans nor
LLMs solve alone and compares the team against both [12], and Collaborative Gym evaluates agents that work with real or simulated users on both outcome and process [19]. Neither addresses visualization design, and, to our knowledge, neither measures whether the agent retains what the human taught it across sessions—the axis our problem class makes central. None of these constructs has an operational counterpart in visualization-agent evaluation.
Why the Problem Class Matters
Why insist on collaboration-level evaluation here—in high-dimensional abstract data—rather than wherever agents are strongest? Because the need follows from the structure of the problem class. Table 1 contrasts scientific visualization, where agent benchmarks are most developed, with high-dimensional abstract data, exemplified by parallel-coordinates (PCP) design over multivariate process data.
| Scientific vis. | High-dim. abstract data | |
| Design space | Continuous (camera, transfer function, isovalue) | Combinatorial (axis subset, ordering, inversion, scaling) |
| Grounding of “good” | Spatial referent in the data itself | Task-relative only |
| Expertise | Largely domain-general; plausibly present in pretrained models | Site-specific, non-transferable |
| Interaction semantics | Navigation | Direct manipulation = design decision |
| ⇒ Feedback lifecycle | Test-time adaptation suffices | Must be distilled and retained |
Table 1. Structural differences between the problem classes. Each row feeds the next; the final row is the premise of our framework.
The rows are causally ordered, and each one dictates something the evaluation must measure. A combinatorial space cannot be searched by the expert alone, yet without a spatial referent the agent cannot tell a good view from a bad one; so the question is whether the pair beats each member (axis 1). Expert attention is the scarce resource in that search, so its cost must be counted (axis 2). Since the expertise is site-specific—which variables matter in this plant, this line, this week [11]—the agent’s proposals cannot be checked against general knowledge, and whether the analyst accepts them for good reasons becomes a question in itself (axis 3). Because that expertise is absent from the model, it must be kept across sessions, so whether the agent needs less correction over time is measurable and matters (axis 4). Finally, it is expressed by direct manipulation—reordering an axis is a design judgment [6]—so the interaction log is where all of this becomes observable.
The Five-Axis Framework
Table 2 summarizes the framework: each axis answers one question about the team under an operational definition over concrete data.
| Axis | Question | Operationalization | Primary data |
| 1. Attainment & complementarity | Does the team beat both solos? | interaction log | |
| 2. Efficiency & intervention budget | At what human cost? | interventions-to-attainment; marginal gain per intervention | interaction log |
| 3. Appropriate reliance & fixation | Blind following? Narrowed search? | acceptance rate split by proposal correctness; design-space coverage | interaction log |
| 4. Knowledge retention | Does the agent need less correction over time? | expert-alignment after distillation; interventions needed in session | logs across sessions |
| 5. Agency, trust, load | Will experts keep using it? | CSI, trust calibration, NASA-TLX | questionnaire |
Table 2. The five-axis framework. Axes 1–4 are computed from interaction logs; axis 5 requires post-session questionnaires.
Axes 1–3. Table 2 carries the operational definitions; three points need stating. With the task loss under condition , complementarity requires [9]—deliberately strict, since a team merely matching the better solo member does not justify its coordination cost. Efficiency counts intervention events
(rejections, manual reorderings, axis substitutions) and reports interventions-to-attainment alongside marginal improvement per intervention , a budget–performance curve whose saturation characterizes how far human attention goes; attainment alone hides human cost. Reliance splits the analyst’s acceptance rate by whether the proposal was in fact correct, separating over-reliance (accepting wrong proposals) from under-reliance (rejecting right ones) [18, 8], paired with design-space coverage—axis-subset diversity relative to trials spent—to capture fixation [22].
Axis 4: Knowledge retention. The distinguishing axis for our problem class (§ 3) and the visualization counterpart of readiness’ learning-over-time family [10]: after distilling one session’s accepted and rejected judgments into the agent, does the next session need fewer interventions to reach the same attainment? We measure session with and without distillation.
Axis 5: Agency, trust, and load. Sustained adoption depends on the expert’s sense of agency and calibrated trust; we adopt standard instruments (CSI, trust calibration, NASA-TLX). This axis requires human participants and is out of scope for the pilot.
Testbed and Pilot Study
The testbed implements the propose–respond loop for PCP design (Figure 1): an agent proposes candidate views, a simulated analyst accepts, rejects, or modifies them, and both actors’ actions are logged. Axes 1–4 are then computed from that log. Its purpose is to check the measures: because we set the simulated analyst’s behavior, we know what each measure ought to report and can check that it does.

Figure 1. Testbed architecture. The dashed region is one session. Neither actor sees what the other knows—the agent has summary statistics and correlation structure but no labels and no , the analyst only and a noisy percept of render quality. All four axes are computed downstream from the event stream (§ 5.4) and alone, never from simulator state, so the metric code runs unchanged on a human-study log.
Task and data
We use the UCI SECOM dataset [15]: 1,567 production runs from a semiconductor line, 590 sensor features, pass/fail labels. The task is to identify, via PCP inspection, the feature subset discriminating failures. Since true physical causes are unknown, we operationally define ground truth as a subset derived beforehand by supervised analysis: stability selection with -regularized logistic regression over 100 bootstrap resamples, then greedy forward selection on nested cross-validated AUC, giving features at AUC —a proxy, not physical truth (§ 7). Preprocessing removes columns more than 50% missing, constant and quasi-constant columns, and one side of every feature pair with , leaving of the 590 features over 1,567 runs with 104 failures (6.6%).
Design space and agent
A candidate PCP view is a tuple : an axis subset with , an ordering , per-axis inversion flags , and per-axis scalings , so the design space has size —approximately candidates at , —the concrete instance of Table 1’s first row. The agent is deliberately two-layered. Every headline number below comes from a rule-based proposer that samples axes from label-free structure heuristics (variance, outlier rate, correlation centrality, Laplacian score) then hill-climbs order, orientation, and scale on a label-free readability score; running sessions through a language-model API is not tractable. A prompt-based LLM proposer (gpt-5.4-mini) implements the identical interface, and § 6 reports a three-cell replication. Because SECOM sensor names are anonymous numeric identifiers, a pretrained model has no semantic prior to exploit—itself an instance of the argument in § 3 that site-specific knowledge of which variable matters is exactly what pretraining does not supply.
Simulated analyst
The simulated analyst is not a substitute for participants. Unlike a simulator standing in for the user being evaluated [16], it does not replace the object of measurement; it calibrates the instrument.
The policy has three parameters in : expertise (fraction of known), reliance (propensity to accept proposals), and exploration (propensity to try candidates beyond proposals). Sweeping reliance is what lets axis 3 separate over- from under-reliance—the pilot’s central device.
Five conditions; no human takes part in any of them. C0, a sanity check pairing random proposals with an accept/reject-only analyst—if this “team” scored as complementary, the metric would be broken; C1 analyst-solo (the simulated analyst with no agent proposals), C2 agent-solo (agent plus automated judge, no analyst), C3 collaboration (propose–accept/reject/modify), and C3′ collaboration whose judgments are not carried to the next session (ablation for axis 4).
Provenance schema
Every condition emits one event stream:
event = {t: float, session_id: str, trial: int,
actor: "agent" | "analyst" | "judge",
action: "propose" | "accept" | "reject" |
"reorder"
| "drop" | "add" | "scale" | "flip" | "
brush"
| "filter" | "conclude",
target: {...}, params: {...},
candidate_id: str, meta: {...}}
Put plainly, axes 1–4 are computed from user logs: the metric code reads only these events (plus to score loss), never the simulator’s internal state, so it runs unchanged on logs from a human study. The meta field, which holds simulator internals such as perceived quality, is excluded for the same reason. The same accept/reject events are also what the agent distills into memory for the next session, so logging serves both evaluation and learning.
Results
For each axis we ask two questions: can it be computed from the log, and does it separate conditions that we know, by construction, to differ? We make no claim that collaboration helps people; a simulator cannot establish that. The grid crosses expertise and reliance with exploration over 30 seeds, 30 trials per session and a hard budget of 30 interventions: 4,980 sessions, 120,755 distinct designs, 177 s on one core. The attainment threshold was fixed in advance from a separate pilot sweep (seeds 0–4, excluded here). We report bootstrap 95% CIs over seeds and no -values, since on a simulator sample size is a free parameter. Table 3 collects the numbers; the text gives the takeaway per axis.
| Axis: measure (from the log) | C0 random | C1 analyst-solo | C2 agent-solo | C3 collab. | Evidence of discrimination |
| 1: mean at conclusion | .734 [.732,.736] | .456 [.454,.459] | .612 [.595,.628] | .468 [.466,.470] | all four CIs disjoint |
| 1: grid cells where team beats both solos | 0% | — | — | 34.7% | C3 by expertise 0/.25/.5/.75/1: 93/80/0/0/0% |
| 2: over first 5 interventions | .013 | .085 | — | .066 | return per intervention differs by condition |
| 2: interventions until the curve saturates | 16 | 6 | — | 8 | sharp knee; C0 saturates late at a poor loss |
| 3: over-/under-reliance as goes 01 | — | — | — | 01 / 10 | cross at : injected reliance read back |
| 3: distinct axis sets / share of features seen | 29.9 / 59% | 7.4 / 2.6% | 5.7 / 13% | 19.1 / 18% | analyst-solo search is narrow (fixation) |
| 4: interventions to , session 15 | — | — | — | 2.180.70 | C3′: 1.952.47; slope diff. −0.44 [−0.50, −0.37] |
Table 3. Pilot results (simulated analyst). is a loss: lower is better. Brackets: bootstrap 95% CIs over seeds. “—”: undefined for that condition (C1 has no proposals to rely on; C2 spends no interventions). The last column is the evidence that the axis discriminates.
Axis 1: complementarity is computable and has a visible boundary. The measure is the loss of the best design the analyst endorsed. All four condition means separate cleanly (Table 3; Figure 2a), but they are not a ranking: they average over different parameter cells, and a fifth of C3’s cells sit at reliance , where the analyst accepts the first proposal and is effectively C2 (dropping them moves C3 to 0.436, below C1). We therefore compare cell by cell. The team beats both solo baselines in 34.7% of cells, all at low analyst expertise; at expertise the simulated analyst does better alone—a boundary we report rather than suppress. Part of it is built in (an analyst holding all of knows exactly what the loss scores), and part is a mechanism worth testing with people: the agent’s tidy layouts raise perceived quality, so the analyst stops early. The random-proposal control C0 is never complementary, so the effect is not a metric artifact.
Figure 2. Pilot results for axes 1–4 (values in Table 3). (a) at conclusion by condition; marginals over different parameter cells, so not a ranking. (b) running-best against interventions spent; C2 is a reference level. (c) over- and under-reliance (both errors) against the injected acceptance propensity at expertise . (d) interventions to reach across five sessions, with (C3) and without (C3′) carried-over judgments. Intervals are seed-to-seed variation in the simulator, not inference about people.
Axis 2: the cost of human attention has a measurable knee. The measure is the running-best loss against interventions spent. C1 and C3 gain most from the first few and saturate sharply (at 6 and 8); C0 gains little and saturates late (Figure 2b). The curve has a readable knee, so “how much analyst effort did this team need?” has a concrete answer.
Axis 3: the measure reads back the reliance we injected. The measure splits acceptances by whether the proposal was in fact good (below ; 52% were). Sweeping the analyst’s acceptance propensity , over-reliance (accepting bad proposals) rises from 0 to 1 while under-reliance (rejecting good ones) falls from 1 to 0 (Figure 2c). That the curves follow is the intended calibration, not circularity: the instrument recovers a disposition whose true value we set. The separation is cleanest without analyst expertise; with expertise, under-reliance barely varies with (its range shrinks to 0.09–0.14), so the separation is itself expertise-dependent. Coverage adds a fixation signal visible in the log alone: analyst-solo search revisits a small familiar set of axes.
Axis 4: retention separates from mere drift only with the ablation. The measure is the number of interventions needed to reach in each of five successive sessions, run on successive time blocks of the data. With the analyst’s judgments carried forward (C3) this falls from 2.18 to 0.70; without them (C3′) it does not fall (Figure 2d), and the difference in slopes has a CI well below zero. The ablation is necessary: blocks differ in failure count (44, 21, 11, 11, 17), so a falling C3 curve alone could mean easier blocks.
Robustness. With an alternative ground truth chosen by mutual information, sharing no features with , the axes still separate the conditions. Reweighting the quality score keeps that separation but can flip C1 versus C3: weighting readability and scale at 0.60 instead of 0.40 puts C3 ahead and doubles the complementary region to 67% of cells, so whether collaboration “wins” partly depends on the weights. The agent’s label-free heuristics recover 2 of the 8 features (chance: 0.23), so C2 is a real baseline.
The measures do not depend on the agent. Replacing the rule-based proposer with an LLM (gpt-5.4-mini) on three cells five seeds leaves every axis computable and orders the cells identically (rank agreement 1.0, no malformed proposals; mean loss 0.469 vs. 0.421). Responses are cached by prompt (49 distinct prompts in 15 sessions), so seed variance there is understated; this is not a comparison of agents.
Limitations and Research Agenda
What this paper shows, and what it does not. Four measures of analyst–agent collaboration can be computed from logs and respond correctly to differences we control; whether they say anything useful about real analysts, who anchor, fixate, and learn, is untested. (1) No human participants: axis 5 is unvalidated and axes 1–4 are validated only as instruments, not as findings about people. (2) SECOM’s is a derived proxy, so attainment means agreement with a supervised analysis. (3) The simulated analyst’s parameters are design choices, not fitted to human data. (4) Collaboration here means persisted corrective feedback; richer forms such as joint exploration or dialogue would need further measures.
Agenda. The next step is a human study using the testbed’s pre-specified metrics. Which axis should be validated with experts first? Complementarity is the headline construct; retention is the one agent-only benchmarks cannot see.
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