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What's the Difference? Voice Design and Confirmation Bias in AI-Assisted Self-Diagnosis: Anthropomorphic vs. Machine-Like Voice Output

Abstract

As symptom checkers based on artificial intelligence (AI) are becoming common entry points for health information, their influence on lay users' diagnostic decisions raises questions about trust and bias. Of particular concern is confirmation bias, the tendency to favour information that supports one's existing belief while discounting information that contradicts it. One of the central design choices for such systems is the style of voice: whether they should present themselves with a human-like (anthropomorphic) or a clearly machine-like (xenomorphic) voice. This study investigates whether the voice design of an AI symptom checker modulates confirmation bias in self-diagnosis. In a within-subjects online experiment (N = 81 participants, 648 trials), participants selected a diagnosis and rated their confidence, then heard an AI-generated recommendation that either confirmed or contradicted their initial choice, delivered by an anthropomorphic or a machine-like voice, before deciding again. We observed a strong, direction-dependent influence of the AI: participants revised their diagnosis in 45.7% of trials when the AI contradicted them versus 1.2% when it confirmed them (generalised linear mixed model, GLMM, p < .001); confidence rose under confirmation but barely moved under contradiction (robust linear mixed model, p < .001); and decisions took longer after contradiction (Gamma GLMM, p < .001). This effect did not differ between the two voices (no voice or interaction term was significant, smallest p = .282), even though a manipulation check confirmed the voices were perceived as markedly different. The findings suggest that the direction of an AI recommendation, rather than the anthropomorphism of its voice, drives confirmation-related bias in AI-assisted self-diagnosis.

CCS Concepts

• Human-centered computing → Empirical studies in HCI; Natural language interfaces; • Applied computing → Consumer health; • Computing methodologies → Artificial intelligence.

Introduction

Symptom checkers based on artificial intelligence (AI) are increasingly used as accessible tools for preliminary health assessment. By allowing users to enter symptoms and receive possible diagnoses or triage advice, these systems may support early orientation before professional consultation. However, prior research has raised concerns about their diagnostic reliability, safety, and suitability for laymen [1, 2].

In medical decision contexts, the interaction between human judgement and AI recommendation is particularly sensitive. Users may not only benefit from AI support but also become vulnerable to automation bias, relying too strongly on automated recommendations even when they are wrong [3, 4, 5].

Such reliance is further shaped by cognitive biases, that is, systematic deviations from rational judgement that arise from the way people process information. One of the most studied biases is confirmation bias, the tendency to seek out, weigh more heavily (i.e., perceive as higher in quality), and more readily accept information that is consistent with one’s prior beliefs while discounting information that contradicts them [6]. In self-diagnosis contexts this bias is particularly relevant: users typically form an initial assumption about their symptoms, and they may therefore be more likely to accept AI feedback that supports that assumption than feedback that challenges it. This carries a concrete risk: when both the user and the AI are wrong, an agreeing recommendation can produce a false confirmation [7]. A layperson may, for instance, be falsely reassured that their symptoms do not require immediate medical attention and therefore fail to seek help in time.

Voice-based AI assistants add another layer to this interaction: spoken recommendations are not perceived as neutral information, since vocal characteristics shape perceived credibility, social presence, and trust [8], and trust in healthcare voice assistants has been shown to depend on perceived usefulness, content credibility, service quality, and risk-related factors [9]. This raises a central design question: whether patient-facing AI should imitate human interaction or present itself as clearly non-human. Anthropomorphic design is often pursued precisely to make a system feel familiar and to engender trust; a machine-like (xenomorphic) design instead emphasises the system’s artificial nature and may reduce patient confusion by clearly distinguishing AI from human physicians [10].

While previous work has examined the accuracy of symptom checkers and trust in healthcare voice assistants, less is known about how the voice design of an AI symptom checker influences users’ diagnostic decisions after confirming or contradicting advice. This study addresses that gap, testing whether users exhibit a general confirmation bias toward the AI - across diagnostic choice, confidence, and response time - and, as its primary question, whether the strength of that bias is moderated by the AI’s voice design (anthropomorphic vs. machine-like). The formal hypotheses are stated in the Methods section.

This paper makes three contributions: (i) a controlled within-subjects design that isolates the direction of an AI recommendation from its vocal presentation in a self-diagnosis task; (ii) mixed-effects evidence for a strong, direction-dependent confirmation bias across choice, confidence, and response time; and (iii) the finding that this bias is unaffected by whether the AI speaks with an anthropomorphic or a machine-like voice, despite a successful perceptual manipulation.

Related Work

Confirmation Bias in AI-Assisted Decision-Making

In his comprehensive review, Nickerson [6] characterises confirmation bias as a pervasive and largely unintentional feature of everyday reasoning rather than a deliberate strategy, spanning biased search for information, biased interpretation of ambiguous evidence, and biased memory.

The strength with which the bias operates is not fixed but modulated by several factors. Four conditions in particular make it stronger: a firm prior commitment to the initial belief, which raises the psychological stakes of maintaining it; evidence that is ambiguous enough to be read as supportive; a source perceived as credible or trustworthy; and a personal motivation to reach a particular conclusion [6]. These moderators matter directly for AI advice: an AI recommendation is an external piece of evidence that a user must integrate with an already-formed belief, and its perceived credibility and the ambiguity of the underlying symptoms determine how readily it is accepted or resisted.

In AI-assisted self-diagnosis this bias is particularly relevant, because users often enter the interaction with an initial assumption about their symptoms. When an AI recommendation agrees with that assumption, users may become more confident in their initial diagnosis even if alternative explanations remain plausible; a contradicting recommendation may instead be discounted because it conflicts with a prior belief. Confirmation bias thus provides a theoretical basis for studying how users react to confirming versus contradicting AI advice.

Empirically, this bias has been observed in each of the three outcomes we examine. For choices, mental-health professionals and students who had first made a preliminary diagnosis of a clinical vignette rated a mock AI triage recommendation as more trustworthy and were more likely to accept it when it matched that diagnosis [11]. For confidence, agreeing advice raises confidence even when it barely changes the judgement itself: in judge–advisor studies with numeric estimates, advice close to one’s initial estimate acts as social validation that increases confidence, an effect that shrinks and eventually vanishes as advice moves further away [12]. People place confidence even in a spurious consensus of redundant, agreeing opinions, whereas they discount independent opinions that conflict with one another, so that confidence and accuracy dissociate [13]; and when participants could adjust an incentivised confidence wager after seeing a partner’s judgement, agreement raised confidence more than disagreement lowered it, and participants took the strength of confirming but not disconfirming opinions into account [14]. Comparable agreement effects occur with AI advice: participants who agreed with participants’ initial judgement led to larger increases in their certainty, and once heeded it was used similarly whether it was labelled as coming from an AI or from peers [15]. Decision time has been studied less directly. Conflicting information can prolong decisions - decision makers spent more time per decision when a peer’s second opinion frequently disagreed with the AI’s recommendation [16] - and time constraints increase anchoring on AI advice: participants given 25 rather than 10 seconds disagreed more often with incorrect AI predictions [17], consistent with fast decisions reflecting less deliberate processing of the advice. Together, these findings lead us to expect that contradicting AI advice triggers more revisions, a weaker increase in confidence, and longer deliberation than confirming advice.

AI-Based Self-Diagnosis and Healthcare Chatbots

AI-based self-diagnosis tools and healthcare chatbots are increasingly used as accessible, immediate sources of health information and preliminary guidance. Yu and Chen [18], for example, examine the acceptance of healthcare chatbots among older adults with an extended UTAUT model and show that performance expectancy, effort expectancy, and social influence shape the intention to use such systems. At the same time, using AI for self-diagnosis introduces risks. Zada et al. [19] investigate medical misinformation in AI-assisted self-diagnosis and find that AI-generated medical advice is often unclear or inaccurate, so that relying solely on such systems for self-diagnosis increases the risk of being misinformed.

This lack of expertise is what makes medical decision-making especially difficult for laypeople. Unlike clinicians, lay users have no formal training to interpret symptoms, to weigh competing differential diagnoses against one another, or to judge how reliable a given AI output is for their particular case [2, 20]. As a result they have few independent grounds on which to check a recommendation, which makes them more dependent on - and correspondingly more swayable by - whatever the system suggests, and less able to detect when its advice is wrong - a concern given that such advice is often unclear or inaccurate [19].

Accuracy and Safety of AI Symptom Checkers

The safety of AI-based self-diagnosis depends on more than technical performance; it also depends on how users interpret and act on system outputs. Mentzou et al. [2] review digital self-diagnosis tools and highlight important gaps in their development, impact, and oversight, so accuracy and safety cannot be judged through diagnostic correctness alone. Capability is rising: Tu et al. [21] present AMIE, a conversational diagnostic AI with strong performance in simulated consultations, yet such controlled results do not represent everyday symptom-checker use by laymen. You and Gui [20] further found that chatbot-based symptom checkers often lack support for comprehensive histories, flexible input, and diverse users, and warn that users may be at risk if they blindly trust the results. The design of the interaction itself may thus influence whether users understand, trust, and follow AI-generated advice.

Biases in AI-Assisted Medical Decision-Making

Beyond accuracy, AI recommendations can shape human decisions. Automation bias refers to the tendency to rely too strongly on automated recommendations even when they may be incorrect. Kücking et al. [3] studied automation bias in AI-based clinical decision support and found that non-specialists were especially susceptible to accepting incorrect AI recommendations. We expect this susceptibility to be even more pronounced in the everyday use of symptom checkers by laypeople. Preliminary evidence from Qazi et al. [4] suggests that even medically trained, AI-literate users can be affected by erroneous large-language-model recommendations in diagnostic reasoning.

Closely related to the present study, Rosbach et al. [7] show - in computational pathology - a direct confirmation-bias effect of AI advice: when an AI recommendation mirrored a pathologist’s own flawed tumour-percentage estimate, that erroneous estimate was reinforced rather than corrected, an effect the authors term false confirmation, and one that time pressure, counter-intuitively, weakened rather than worsened. This maps directly onto the situation we study, in a lay self-diagnosis rather than an expert pathology setting: an AI recommendation that agrees with a user’s initial diagnosis, whether right or wrong, may entrench it in the same way, which is exactly the mechanism our confirming condition isolates - underscoring, together with broader analyses of bias in medical AI [22], that the risks of AI-assisted diagnosis depend not just on system accuracy but on how users respond when an answer confirms or contradicts their own judgement.

Voice Design, Anthropomorphism, and Machine-Like AI

How AI advice is presented may further affect perception and decision-making. In voice-based systems the recommendation is processed as speech and not merely as text, and vocal characteristics can influence how confident, credible, or socially present a system appears. Kridlund et al. [23] show that speech features such as filled pauses, speech rate, and fundamental frequency affect perceived speaker confidence, suggesting that users read acoustic properties as cues to certainty or reliability. More broadly, a survey of voice in human–agent interaction reports that human-like voices are generally rated as more likeable and often as more trustworthy or credible than synthetic ones, whereas evidence for behavioural consequences such as persuasiveness is inconsistent [8]. Voice design may therefore affect decisions independently of content: Dubiel et al. [24] found that synthetic voice quality influenced participants’ choices even when the available options were held constant, and frame this as a potential dark pattern. A related question is whether medical AI should appear human-like or clearly non-human. Milford et al. [10] argue against anthropomorphism in patient-facing medical AI and advocate a xenomorphic approach that emphasises non-human characteristics to distinguish AI from human physicians, arguing that human-like designs built on trust-engendering features fall into the uncanny valley, import cultural biases about who appears trustworthy, and risk competing with the human doctor–patient relationship. Beyond being a mere presentation choice, anthropomorphism may thus itself act as a bias: attributing human traits, credibility, or agency to a system can shape trust independently of the actual content of its advice. Such attributions are not neutral, either: anthropomorphic conversational assistants are frequently gendered: even where companies claim otherwise, system outputs are ambiguous about their humanness and users personify and gender them [25]. This distinction matters in healthcare, where human-like systems may increase trust but also blur the boundary between automated advice and professional medical judgement. In line with this literature we operationalise the non-human design as a machine-like voice and contrast it with an anthropomorphic one.

These strands - confirmation and automation bias in AI-assisted diagnosis, the particular vulnerability of laypeople, and the perceptual effects of voice design - have rarely been combined, leaving open whether the voice of an AI symptom checker modulates how strongly users maintain or revise an initial diagnosis after confirming or contradicting advice: the question the present study addresses.

Methods

Experimental Design

We conducted a within-subjects online experiment crossing two factors: AI condition (whether the AI recommendation confirmed or contradicted the participant’s initial diagnosis) and voice design (whether it was delivered in an anthropomorphic (i.e., human-like) or a machine-like synthetic voice). Every participant experienced all four combinations of the two factors.

Three dependent variables were measured on each trial: whether the participant changed their diagnosis after hearing the recommendation, the shift in their stated confidence, and the response time needed to reach the final decision. Figure 1 summarises the procedure.

Study procedure diagram showing session-level stages and the repeated trial sequence

Figure 1. Study procedure. Top row: the session-level stages, from demographics through a practice trial, the main study (highlighted), and the closing voice ratings. Bottom row: the fixed four-step sequence repeated on each of the eight trials - participants read a symptom vignette, make an initial diagnosis and rate their confidence, hear the AI recommendation (which either confirms or contradicts their pick, green box), and then make their final diagnosis and confidence rating. The eight trials are split into two counterbalanced voice blocks of four, each containing two confirming and two contradicting recommendations. The initial-vs.-final decision difference is the bias effect analysed throughout.

We tested two hypothesis sets: the first, a general confirmation bias toward the AI across the three outcomes:

H1a Participants change their diagnosis more often when the AI contradicts their initial choice than when it confirms it.

H1b A confirming recommendation increases confidence relative to a contradicting one, i.e. the confidence shift is more positive after confirmation.

H1c Participants take longer to reach their final decision after a contradicting recommendation than after a confirming one.

The second, primary hypothesis concerns whether the AI’s voice moderates this bias, and in which direction:

H2 The strength of the confirmation-bias effect (H1a–H1c) differs between the anthropomorphic and the machine-like voice.

H2a The confirmation-bias effect is stronger for the anthropomorphic voice than for the machine-like voice, as human-like delivery is expected to raise the perceived credibility of the recommendation.

Participants

The final sample consisted of 81 participants who completed the study (648 analysed trials); sixteen were recruited during a live event and received a slice of pizza as compensation, the remainder through convenience sampling within the researchers’ extended personal networks. Five sessions that were started but not completed were excluded; the sample’s demographic composition is reported with the results (see Sample at the start of the Results).

Materials and Apparatus

The diagnostic cases were short patient vignettes constructed by the research team from the disease–symptom associations of a publicly available, artificially generated dataset covering 773 diseases and 377 symptoms [26]: each vignette describes the symptoms the dataset lists for one disease, written by the authors in everyday language so that laypeople could reason about them without specialist knowledge. Each vignette was followed by three diagnostic options: the disease the symptoms were drawn from and two alternative diagnoses that the authors judged plausible for the described symptoms. As the authors are not medical professionals, the cases were not clinically validated. Instead, the vignettes and options were piloted with peers to ensure that they were understandable and that none of the options appeared implausible. The study therefore does not rely on the medical correctness of any option: the manipulation concerns whether the AI confirms or contradicts the participant’s own initial choice, and no option was scored as correct in the analysis. The pool comprised twelve vignettes; to broaden the stimulus set without lengthening the sessions, each participant received a seeded random subset of eight, and case was modelled as a random effect in all analyses. The participant-facing interface is shown in Figure 2.

AI recommendations were pre-scripted by the authors rather than produced by a live model, so that the verbal content was held constant across participants and only the voice varied. For every option of every case, the authors wrote a short German explanation of two to three sentences that named the diagnosis and related it to the described symptoms (e.g., that the symptoms began directly after a large meal, which is typical of the recommended diagnosis); these texts were then synthesised into speech with the two voices described below. For each option the spoken content was identical across the two voices; the voices differed only in their acoustic delivery.

The anthropomorphic voice was synthesised with ElevenLabs’ neural text-to-speech (TTS) service (model eleven_v3, a custom female voice created with ElevenLabs Voice Design), configured for expressive delivery (stability 0.35, similarity boost 0.75, style 0.45, speaker boost enabled) and enriched with natural delivery cues: audible breaths and hesitation fillers (e.g. “ähm”). The machine-like voice was synthesised with Microsoft Edge TTS (voice de-DE-KatjaNeural), rendered with a lowered pitch (−30 Hz) and slightly reduced rate (−5%) to emphasise a flat, plainly synthetic character, and read the same content without any delivery cues.

The two voices were thus intended to contrast human-like prosody and warmth against flat, mechanical delivery. To ensure this was a contrast of character rather than level, all audio was loudness-normalised to −16 LUFS (EBU R128) with ffmpeg (loudnorm, I=−16I = -16, TP = −1.5, LRA = 11).

The study ran in the browser on both desktop and smartphone, and participants were advised to use headphones for consistent audio playback.

Procedure

Before the main experiment, participants provided demographic information (age and gender) and reported their prior experience with AI symptom checkers and AI voice assistants. A single practice trial with one additional vignette then familiarised them with the task and was excluded from analysis.

For each case, participants first read the patient vignette, selected the diagnosis they considered most likely, and rated their confidence on a 7-point Likert scale from 1 (very low) to 7 (very high). They then listened to the AI voice recommendation, after which they again selected one of the three options and re-rated their confidence. Response times were recorded both before and after the recommendation.

The participant-facing interface of the study application

Figure 2. The participant-facing interface of the study application (in German, as presented to participants), illustrating the four key screens of a trial: (a) the symptom vignette describing the patient case; (b) the initial diagnosis choice among three options; (c) the seven-point confidence rating (anchored unsicher/unsure to sehr sicher/very sure); and (d) the spoken AI recommendation, presented as audio playback without on-screen text. After the recommendation, participants repeated screens (b) and (c) for their final decision.

Each participant’s eight cases were split into two blocks of four, one block per voice, with a short break between the blocks. Each participant thus heard one voice throughout the first block and the other throughout the second, with no mixing of voices within a block.

Trial assignment was generated deterministically from a per-session seed, which makes each session fully reproducible and exactly counterbalanced. A seeded pseudo-random generator (Mulberry32, seeded via an FNV-1a hash of the session identifier) drove all randomisation. The participant’s eight cases were sorted into four pairs, each pair’s coin flip assigning its two cases to opposite AI conditions - yielding exactly four confirming and four contradicting trials per participant. Block order (anthropomorphic-first vs. machine-first) was likewise coin-flip balanced; each block received two confirming and two contradicting cases, shuffled within the block to reduce presentation-order effects.

After completing all trials, participants heard a short sample of each voice again and rated it on eight 7-point semantic differentials, which served as a manipulation check. Human-likeness (machine-like–human-like), naturalness (artificial–natural), pleasantness (unpleasant–pleasant), and competence (incompetent–competent) were single items adapted from the anthropomorphism, likeability, and perceived-intelligence scales of the Godspeed questionnaire [27], which was developed for robots and uses 5-point scales; the naturalness item combines its fake–natural and artificial–lifelike pairs. Trustworthiness and intelligibility followed subjective rating studies of synthetic voices [28], warmth (distant–warm) was added following the warmth–competence framework of social perception [29], and a final item captured whether the voice sounded male or female. All items were presented in German translations by the authors, in randomised order. As this set is an ad-hoc adaptation rather than a validated scale, we analysed the items individually.

Measures and Analysis

The three dependent variables were operationalised from the per-trial records. Diagnosis change was a binary indicator that the final diagnostic choice differed from the initial one. Confidence shift was the difference between the post- and pre-recommendation confidence ratings on the 1–7 scale. Final-decision response time was the time, recorded in milliseconds and reported in seconds, from the moment the answer options reappeared - i.e., after the recommendation had finished playing and the participant had continued - to the final diagnostic choice. Because the study ran unsupervised in the browser, these times also include any moments in which a participant was not attending to the task (see Limitations).

We analysed the trial-level data (648 trials) with one mixed-effects model per outcome, each with fixed effects for AI condition, voice, and their interaction and crossed random intercepts for participant and case. Both factors were coded with sum-to-zero contrasts (confirming AI condition and machine-like voice as the positively signed levels), so that each main effect is averaged over the levels of the other factor. Diagnosis change was modelled with a binomial generalised linear mixed model (GLMM, logit link) [30]. For the two continuous outcomes, the residuals of Gaussian linear mixed models (LMMs) deviated clearly from normality, with heavy tails for the confidence shift and a pronounced right skew for response time even after log transformation (Shapiro–Wilk W = 0.975 and W=0.896W = 0.896, both p<.001p < .001; Q–Q plots in Appendix § 8). We therefore modelled the confidence shift with a robust LMM, which down-weights outlying observations [31], and response time with a Gamma GLMM with log link on untransformed seconds [32, 33], which accommodates the right-skewed distribution of response times without transforming the outcome. For the confidence shift, the variance of the case intercept was estimated at zero (singular fit), i.e. the shift did not vary systematically between cases; this leaves the fixed effects unaffected.

From each model we derived estimated marginal means for the four AI × voice cells and the contrasts of interest on the model’s natural scale: the odds ratio of a diagnosis change (contradict vs. confirm), the difference in confidence shift (confirm − contradict, in scale points), and the ratio of mean response times (contradict / confirm). Voice moderation (H2) was tested by the AI × voice interaction, expressed as the difference between the AI effects under the two voices. All tests and 95% confidence intervals (CIs) are Wald-type. As sensitivity checks, we refit the two continuous outcomes with the Gaussian LMMs used in an earlier version of this analysis (Appendix § 9) and ran participant-level nonparametric tests on aggregated data (Appendix § 10).

Ethical Considerations

Participation was voluntary and anonymous: no clinically identifying information was collected, and participants could abort at any time without giving a reason. Because the AI recommendations were simulated and deliberately contradicted participants on half of the trials, every participant received a debriefing explaining that the recommendations had been pre-configured and did not constitute medical advice; the use of vignettes adapted for laypeople, rather than participants’ own health data, further limited any risk.

Results

This section first describes the sample and then reports our two sets of hypotheses: a general confirmation bias toward the AI (H1a–H1c) and the moderating role of voice design (H2).

Sample

All 81 participants who completed the study were included (Figure 3). The sample was roughly balanced by gender and skewed young (85% under 35). The two block orders were represented in similar numbers: 39 participants heard the anthropomorphic voice first and 42 the machine-like voice first. Participants reported little prior experience with AI symptom checkers or voice AI assistants, with both medians at the lower end of the 1–7 scale (median 3).

Sample overview showing gender, age, block order, and prior experience

Figure 3. Sample overview (N=81N = 81). The stacked bar chart shows the composition of the sample by gender, age band, and counterbalanced block order (each bar sums to 100 %, with the within-segment percentages printed inline); the bottom row places the median (filled dot) and mean (open diamond) of prior experience with AI symptom checkers and voice assistants on the 1–7 scale.

General Confirmation Bias (H1)

Full model coefficients are reported in Table 1 and model-based estimates for each condition in Figure 4.

(A) Diagnosis change (binomial GLMM, logit link)
TermbbSEzzppebe^b [95% CI]
Intercept−2.9760.395−7.54<.0010.05 [0.02, 0.11]
AI−2.7190.338−8.04<.0010.07 [0.03, 0.13]
Voice0.2490.3020.82.4101.28 [0.71, 2.32]
AI × Voice0.3250.3021.08.2821.38 [0.77, 2.50]
(B) Confidence shift (robust LMM)
TermbbSEttpp95% CI
Intercept0.3140.0555.75<.001[0.207, 0.421]
AI0.5050.03713.79<.001[0.434, 0.577]
Voice0.0030.0370.09.928[−0.069, 0.075]
AI × Voice0.0110.0370.31.759[−0.061, 0.083]
(C) Response time (Gamma GLMM, log link, seconds)
TermbbSEzzppebe^b [95% CI]
Intercept1.2480.06220.19<.0013.48 [3.09, 3.93]
AI−0.2990.026−11.34<.0010.74 [0.70, 0.78]
Voice0.0160.0260.62.5331.02 [0.97, 1.07]
AI × Voice−0.0210.026−0.81.4200.98 [0.93, 1.03]

Table 1. Fixed-effect coefficients of the three primary models (N=81N = 81 participants, 648 trials; crossed random intercepts for participant and case). Factors are sum-to-zero coded: AIAI = confirm (+1) vs. contradict (−1), VoiceVoice = machine-like (+1) vs. anthropomorphic (−1), so each coefficient is half the difference between the two levels on the model’s link scale. All tests and 95 % CIs are Wald-type.

Three bar-chart panels showing diagnosis changed, confidence shift, and response time by voice and recommendation type

Figure 4. The three trial-level outcomes tested under H1, by voice (x-axis within each panel) and recommendation type (teal = AI confirms, red = AI contradicts; see legend): (a) model-estimated rate of trials on which the initial diagnosis was revised; (b) change in self-reported confidence (post − pre, 1–7 scale); and (c) time to the final decision in seconds. Bars are estimated marginal means from the binomial GLMM (a), the robust LMM (b), and the Gamma GLMM (c), with 95 % CI whiskers; the number above each bar is its point estimate. Model coefficients are given in Table 1.

Diagnostic choice (H1a). The AI recommendation strongly influenced the final diagnosis. Participants changed their diagnosis in 45.7% of trials when the AI contradicted them, but in only 1.2% when it confirmed them (change rate = trials with a changed diagnosis divided by all trials in that condition; Figure 4a). In the binomial

GLMM, the odds of a change were about 230 times higher after a contradicting than after a confirming recommendation (OR = 230, 95 % CI [61, 865], p<.001p < .001; Table 1, panel A). The very wide interval reflects the near-absence of changes under confirmation (see Limitations); the direction and significance of the effect are unaffected. H1a is supported.

Confidence (H1b). A confirming recommendation raised confidence substantially (from 4.46 to 5.42 on the 1–7 scale, a shift of +0.96), whereas a contradicting one lowered it only slightly (from 4.42 to 4.34, a shift of −0.09). In the robust LMM, the confidence shift was 1.01 scale points more positive after confirmation than after contradiction (95 % CI [0.87, 1.15], p<.001p < .001; Figure 4b; Table 1, panel B). H1b is supported. Because confidence after a switch refers to a different diagnosis than before, we repeated the analysis on the 76.5 % of trials on which participants kept their initial pick (robust LMM fitted to these trials only); the difference remained significant and comparable in size (Δ = 1.08, p<.001p < .001).

Response time (H1c). Decisions took markedly longer after a contradicting recommendation. Raw mean decision times were 2.7 s under confirmation versus 6.0 s under contradiction. The Gamma GLMM estimated mean times of 2.6 s and 4.7 s, respectively, i.e. final decisions took 1.82 times as long after contradiction (95 % CI [1.64, 2.02]), p<.001p < .001; Figure 4c; Table 1, panel C), or, equivalently, were 45% faster after confirmation. H1c is supported.

The participant-level nonparametric checks in Appendix C confirm all three effects.

Mean ratings of eight perception items for anthropomorphic and machine-like voices

Figure 5. Manipulation check: mean ratings of the two voices on eight perception items (1–7 scale; blue = anthropomorphic voice, grey = machine-like voice, value printed at each bar’s end; “n.s.” marks the only item without a significant difference between the voices).

Influence of Voice Design

Against our primary hypothesis, the anthropomorphic and machine-like voices produced indistinguishable effects on every outcome. Neither the voice main effect nor the AI × voice interaction was significant in any of the three models (diagnosis change: voice p=.410p = .410, interaction p=.282p = .282; confidence shift: voice p=.928p = .928, interaction p=.759p = .759; response time: voice p=.533p = .533, interaction p=.420p = .420). Table 2 shows the AI effect estimated separately within each voice: it was large, significant, and of similar size for both voices on all three outcomes. For the confidence shift, the difference between the voices’ AI effects was -0.05 scale points (95 % CI [-0.33, 0.24]); for response time, the ratio of the two voices’ AI effects was 0.92 (95 % CI [0.75, 1.13]). Both intervals include no difference and are small relative to the AI effect itself (1.01 points and a ratio of 1.82, respectively), so a moderation of practically relevant size is unlikely for these outcomes. For diagnosis change, the corresponding ratio of odds ratios was 3.66 (95 % CI [0.34, 38.99]); this interval is wide because of the sparse confirm-condition cell. H2 is not supported, and consequently neither is the directional prediction H2a.

Change (OR)Confidence (Δ\Delta)Time (ratio)
Anthropomorphic440 [?, ?]0.99 [0.79, 1.19]1.74 [1.51, 2.01]
Machine-like120 [31, ?]1.03 [0.83, 1.24]1.90 [1.64, 2.19]
Interaction3.66 [0.34, 38.99]−0.05 [−0.33, 0.24]0.92 [0.75, 1.13]

Table 2. Effect of the AI condition within each voice and the difference between voices (interaction), from the primary models with 95 % CIs. Diagnosis change: odds ratio contradict/confirm; confidence shift: confirm − contradict in scale points; response time: ratio of mean times contradict/confirm. For the interaction row, the voice difference is expressed as a ratio of the anthropomorphic to the machine-like effect for odds and time, and as anthropomorphic − machine-like for confidence; no difference corresponds to 1 and 0, respectively.

Manipulation Check

To verify that the two voices were perceived differently, participants rated each voice on a reduced set of Likert items at the end of the study (Figure 5). The anthropomorphic voice was rated significantly more human-like, natural, warm, pleasant, intelligible, and trustworthy, and it sounded more clearly female than the machine-like voice, which was rated near the scale midpoint on the male–female item (all p<.05p < .05). The sole exception was perceived competence, which did not differ between the voices (p=.89p = .89). The manipulation was therefore successful: the null effect of voice on bias cannot be attributed to participants failing to perceive the voices as different. We note, however, that both voices were rated as fairly artificial in absolute terms, a point we return to in the discussion.

Discussion

This study asked whether the voice design of an AI symptom checker influences confirmation bias in AI-assisted self-diagnosis. We found a strong, direction-dependent confirmation effect: participants were substantially more likely to keep their initial diagnosis when the AI confirmed it, while contradicting advice produced more frequent changes and longer response times; confidence, in contrast, rose markedly after confirmation but barely moved after contradiction. This effect did not differ between the anthropomorphic and the machine-like voice.

A Confirmation Bias, Not a Between-Person Artefact

Participants did not treat the AI recommendation as neutral information: its direction shaped both their choices and their subjective confidence. The clearest signature is the asymmetric confidence update: agreement raised confidence substantially (a shift of +0.96 scale points) while disagreement barely moved it (−0.09), the two differing by 1.05 points. This is precisely what confirmation bias predicts - confirming evidence is weighted more heavily than disconfirming evidence, and people preferentially accommodate information that agrees with a belief they already hold [6]. The pattern mirrors advice studies in which a partner’s agreement raised confidence more than disagreement lowered it [14] and people trusted a spurious consensus of agreeing opinions while discounting conflicting ones [13]; in perceptual decisions, high confidence has moreover been shown to selectively attenuate the neural processing of disconfirming post-decision evidence [34]. An updater equally sensitive to both directions of evidence would lower confidence after contradiction about as much as it raises it after confirmation, while a sceptical updater would do neither; our participants raised their confidence after confirmation but barely lowered it after contradiction.

The small average change after contradiction conceals two opposite movements. Participants who kept their diagnosis despite the contradiction lowered their confidence (-0.36 points, 176 trials), whereas those who switched to the AI’s suggestion rated their confidence in the new diagnosis slightly higher than in their original one (+0.24 points, 148 trials). Contradiction therefore did affect participants: it either moderately shook their confidence or led them to adopt the AI’s view with about the confidence they had initially placed in their own. In neither case did it produce a confidence loss comparable to the gain after confirmation.

Crucially, the design rules out the most obvious alternative: because every participant responded to both confirming and contradicting recommendations, the asymmetry is a within-person contrast, not an artefact of stable differences in how readily people revise decisions. A generally reluctant participant would move little in either condition, yet the same people moved far more after contradiction than after confirmation, with the confidence gap holding within individuals once repeated measures were modelled - a property of how each person handled agreement versus disagreement, not between-person heterogeneity in trust or stubbornness.

We are nonetheless careful about the scope of this claim: it characterises the bias at the level of the sample, not each individual as biased, since we did not separate participants by their general tendency to trust or distrust the AI (see Limitations). The high rate of diagnosis changes after contradiction shows that users were also readily willing to abandon their own judgement when the AI offered an alternative - a strong automation-bias signature that echoes concerns about over-reliance on AI advice [3, 4]. Taken on its own, the change rate could therefore be explained by automation bias alone: deferring to the AI produces many changes after contradiction and none after confirmation, regardless of any preference for confirming information. The confidence and response-time results go beyond this. Pure deference would predict comparable updating in both directions, yet confirmation raised confidence substantially while contradiction barely lowered it, and agreeing advice was processed markedly faster than disagreeing advice. Taken together, the three outcomes indicate that confirmation bias, and not only automation bias, shapes how users decide with AI advice.

Why Voice Design Did Not Matter

The absence of a voice effect is the more surprising result, given that our manipulation check confirmed the two voices were perceived very differently on human-likeness, warmth, naturalness, and trust. One explanation is that the content of the recommendation simply dominated its delivery, with acoustic style playing at most a secondary role. This would be in line with findings that advice is used similarly once heeded, whether it is labelled as coming from an AI or from human peers [15], and that human-like voices, while generally better liked, have inconsistent effects on behaviour [8]. A second is that, although the voices differed relative to each other, both were rated as fairly artificial in absolute terms, so the contrast may not have been strong or human-like enough to change susceptibility to the confirmation effect.

Either way, the null carries a design lesson: prior work has warned that anthropomorphic design in medical AI may confuse patients about where automated advice ends and human medical care begins, motivating calls for deliberately machine-like (xenomorphic) systems [10], but our findings show voice style alone did not measurably change susceptibility to confirmation-related bias, while the recommendation’s direction did. Designers should therefore not treat voice style as a primary lever for reducing biased decision-making - the leverage lies in what the system says, not in how human it sounds.

Implications

Our findings matter because symptom checkers are typically used outside professional supervision, where an inaccurate AI can steer laypeople in either direction: a confirming AI can entrench a wrong self-diagnosis through the very confidence boost we observed, while a contradicting AI can just as easily talk a correct user out of it, given the high revision rate we found. In both cases the recommendation’s direction, rather than its accuracy, drives the decision - exactly the failure mode that makes over-reliance on unsupervised medical AI consequential [3, 4, 7, 22].

Because the effect was carried by content rather than voice, mitigation should target the content of the interaction: systems should communicate uncertainty by calibrating expressed confidence to the recommendation’s reliability, prompt users to consider alternative diagnoses instead of presenting a single verdict, use reflective prompts that ask users to consider why their initial guess might be wrong, and carry explicit reminders that AI advice is not a substitute for professional care, especially before a confident-sounding confirmation. Given the null voice effect, these content-level choices matter more than acoustic or anthropomorphic styling: rather than sounding more (or deliberately less [10]) human, patient-facing AI should invest in how it frames uncertainty and invites users to question their own assumptions.

These implications should be read against the profile of our sample, which skewed young (85% under 35). Younger, likely more technology-fluent users may relate to AI advice differently from older populations who make up a large share of real symptom-checker use, so the size - though not necessarily the existence - of the confirmation effect may vary across age groups; we discuss this generalisability question further in the Limitations.

Limitations and Future Work

Several limitations should be considered when interpreting these results. The change rate under confirmation was near zero (4 of 324 trials), so the GLMM’s confirm-vs-refute contrast for diagnostic choice is estimated from a sparse cell and should be read qualitatively rather than as a precise point estimate.

The diagnostic cases were selected and adapted by the researchers, who are not medical experts, so their clinical accuracy and difficulty were not formally validated - less critical for our aim, since we tested whether decision and confidence changed after confirming or contradicting AI advice, not whether participants chose the medically correct diagnosis.

Relatedly, participants reasoned about standardised vignettes rather than their own symptoms. Judging an adapted case is not the same as facing a personal health concern: real self-diagnosis carries emotional stakes that could either sharpen confirmation bias - people may cling harder to a feared or hoped-for interpretation - or weaken AI reliance, if users treat their own bodies as more authoritative than a generic recommendation. Our design therefore has limited ecological validity for how confirmation bias and AI reliance operate when the problem is one’s own.

The study also used preconfigured AI responses rather than a live interactive system. This improved experimental control and held content constant across participants, but reduced ecological validity, as real symptom checkers respond dynamically to user input. The online format added further technical and environmental variability - sessions ran on different devices and in different settings, and although headphones were recommended, listening conditions could not be controlled. A few participants restarted the study after technical issues; their incomplete first sessions were discarded, as were all other incomplete sessions. The unsupervised setting also affects response times: a small number of trials show very long latencies (7 of 648 trials above 30 s, maximum 172 s), most plausibly because participants were briefly distracted (e.g., looked away from the screen) before continuing. The app registered tab switches only during audio playback and cannot detect off-screen attention, so such interruptions could not be identified reliably and no trials were excluded; the response-time model was chosen to be robust to this right tail.

Our analyses characterise the confirmation effect at the level of the sample rather than the individual. The mixed models and paired tests establish that, within participants, contradiction triggered substantially more revision and confidence loss than confirmation; but we did not classify participants by their general disposition to revise decisions or to trust the AI. A participant who rarely changes their mind, or who distrusted the AI throughout, can contribute to the aggregate pattern for reasons other than confirmation bias, and cleanly separating such dispositional differences from a within-person confirmation effect would require more trials per participant and explicit measures of baseline revision tendency and trust.

The sample also skewed young (about 85% under 35) and inexperienced with these technologies (median prior experience 3 on the 1–7 scale), both of which threaten generalisability in ways that could cut either direction: older adults may differ in their familiarity with AI tools, baseline trust, and self-diagnosis habits, so the effect’s size - though probably not its direction - may not generalise to older populations; and while inexperienced users have no calibrated basis for discounting a recommendation, more experienced ones might weigh AI advice differently, whether by trusting or scrutinising it more. The magnitude of the effect may therefore vary across age and experience in ways our sample cannot reveal.

Finally, and most relevant to our main question, the anthropomorphism gap we induced may simply have been too small to move the bias: both voices were AI-generated and, though distinguishable from each other, were rated as fairly artificial in absolute terms. A genuinely human voice might produce a different result - a possibility our design cannot rule out and that bears directly on our central research question.

These limitations point to clear next steps: stronger, differentiated voice manipulations - ideally a genuinely human voice; medically validated cases with participants’ own health concerns, recovering the ecological validity vignettes sacrifice and letting AI direction be crossed with correctness; and a real, dynamic AI chatbot in place of the pre-scripted recommendations used here. Beyond voice, content-level interventions - explanations, calibrated uncertainty, reflective prompts - may reduce confirmation bias and over-reliance, since direction seems to matter more than delivery.

Conclusion

We investigated whether the voice design of an AI symptom checker shapes confirmation bias in lay self-diagnosis. In a within-subjects online experiment (N=81N = 81), AI recommendations exerted a strong, direction-dependent influence: participants changed their diagnosis far more often and deliberated longer when the AI contradicted rather than confirmed them, while their confidence rose substantially only after confirmation (all p<.001p < .001). Contrary to our primary hypothesis, this confirmation effect was statistically indistinguishable between an anthropomorphic and a machine-like voice, even though the two voices were reliably perceived as different. The presence and direction of an AI recommendation thus appear to matter more for confirmation bias than the specific voice style used to deliver it, with the design implications discussed above.

Open Science Statement

All data, analysis code, study materials, and the study application are openly available at https://doi.org/10.5281/zenodo.22770605. The archive contains the study application, the trial-level and participant-level datasets in pseudonymised form together with a full codebook, the raw export prior to cleaning (so that the exclusion of incomplete sessions can be verified), the R scripts reproducing every value reported here, the twelve clinical vignettes with their response options and spoken explanations, and the voice-perception instrument. Data and materials are released under CC BY 4.0, code under the MIT licence.

Condition assignment was generated deterministically from a per-session seed, so the complete assignment for a given session ID (block order, voice per block, case order, and AI condition per trial) can be regenerated exactly from the published code. Session IDs themselves are not published. Running the deposited scripts reproduces the reported model estimates without modification.

Audio stimuli are not redistributed, because the terms of the two commercial text-to-speech services used do not clearly permit it; the generation code, prompt templates, and voice parameters are included so that the stimuli can be regenerated, and the authors will provide the original files on request.

This study was not preregistered.

Acknowledgments

We thank all participants for taking part in the study. Claude (Anthropic) was used to assist with developing the study software, and Gemini (Google) for literature research, proofreading, and translation. All study content, design decisions, analyses, and conclusions were created and verified by the authors.

Residual Diagnostics

To choose appropriate models for the two continuous outcomes, we first fitted Gaussian linear mixed models (LMMs) to the confidence shift and to log-transformed response times and inspected their residuals. Figure 6 shows normal quantile–quantile plots of the conditional residuals of these two models.

Figure 6. Normal Q–Q plots of the LMM conditional residuals for the confidence-shift outcome (a) and the log response-time outcome (b). Points would fall on the diagonal under normality; both show clear departures in the tails, and the response-time residuals remain right-skewed.

Formal Shapiro–Wilk tests reject normality for both outcomes (confidence shift W=0.975W = 0.975, p<.001p < .001; log response time W=0.896W = 0.896, p<.001p < .001), and the Q–Q plots show heavy tails for the confidence shift and a remaining right skew for response time despite the log transformation. Because the Shapiro–Wilk test is very sensitive at this sample size and the confidence ratings are bounded, we use the test only together with the Q–Q plots, as evidence that the normality assumption is not met. This motivated the primary models reported in the main text: a robust LMM for the confidence shift and a Gamma GLMM with log link on untransformed seconds

ModelTermbb [95% CI]pp
Shift, robust LMMAI0.505 [0.434, 0.577]<.001
Shift, Gaussian LMMAI0.523 [0.441, 0.605]<.001
Shift, robust LMMAI × V0.011 [−0.061, 0.083].759
Shift, Gaussian LMMAI × V−0.005 [−0.087, 0.077].912
Time, Gamma GLMMAI−0.299 [−0.351, −0.247]<.001
Time, LMM on logAI−0.250 [−0.299, −0.202]<.001
Time, Gamma GLMMAI × V−0.021 [−0.071, 0.030].420
Time, LMM on logAI × V−0.002 [−0.050, 0.047].937

Table 3. Sensitivity analysis: AI main effect and AI × Voice interaction (sum-coded coefficients bb with Wald 95% CIs) in the primary models and in Gaussian LMMs, which assume normally distributed residuals.

for response time. The diagnosis-change outcome is analysed with a binomial GLMM, which makes no residual-normality assumption.

Sensitivity Analysis: Gaussian LMMs

Table 3 compares the AI main effect and the AI × voice interaction of the primary models with those of Gaussian LMMs fitted to the confidence shift and to log-transformed response times. The conclusions are the same under both model families: the AI effect is large and significant, and the interaction is small and non-significant.

Participant-Level Tests

To check that the trial-level results do not depend on the mixed-model assumptions, we also analysed data aggregated per participant. For diagnosis change, each participant’s proportion of changed diagnoses was computed in each of the four AI × voice cells (two trials per cell) and compared with a Friedman test with participant as the blocking factor; the cells differed significantly (χ2(3)=123.9\chi^{2}(3) = 123.9, p<.001p < .001, Kendall’s W=0.51W = 0.51). Additionally, a McNemar test compared, within participants, whether a person changed their diagnosis on at least one trial under contradiction and under confirmation: 79% of participants did so at least once under contradiction versus 4.9% under confirmation (χ2=58.0\chi^{2} = 58.0, p<.001p < .001). For the confidence shift, a Friedman test on the per-participant cell means likewise showed a significant difference between the four cells (χ2(3)=88.2\chi^{2}(3) = 88.2, p<.001p < .001, Kendall’s W=0.36W = 0.36). Holm-corrected Wilcoxon signed-rank tests trace both Friedman results to the AI condition: the confirm and contradict cells differed within each voice (all p<.001p < .001), whereas the two voices did not differ within either AI condition (all p=.847p = .847 or larger).

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