Designing HRI user studies

Much of what we know about human-robot interaction comes from user studies: experiments and field observations in which people interact with robots and researchers measure what happens. Designing a good study is a skill in its own right. A study that is poorly designed can produce confident conclusions that are simply wrong, waste participants' time and, in the worst cases, expose them to risk without benefit. This lesson covers how to turn a design question into a testable hypothesis, how to choose between study designs, how to control confounds, how to use standard questionnaires such as Godspeed, the NASA-TLX and the System Usability Scale, how to plan sample sizes, and how research ethics review works in Canada and the United States. Lesson 9 then covers how to analyse the data.

From question to hypothesis

A study starts with a question: does a robot that signals its intended path with a floor projection make bystanders feel safer than one that uses only a light ring? To test it, the question becomes a hypothesis with defined variables. The independent variable is what the researcher manipulates: the signalling method, with two levels, projection and light ring. Dependent variables are what is measured: perceived safety on a validated scale, how far people step aside, and how long they hesitate. Confounding variables are anything else that differs between conditions and could explain the result, such as the time of day, the experimenter's behaviour or the robot's speed. A good hypothesis is specific and falsifiable: participants will rate perceived safety higher and hesitate less with the floor projection than with the light ring.

Researchers should state hypotheses and analysis plans before collecting data. Preregistration, publishing the hypotheses, design, sample size and analysis plan in a time-stamped public registry such as the Open Science Framework, helps separate confirmatory tests from exploratory findings and reduces the risk of reporting only the analyses that happened to work. Lesson 9 explains why this matters, in the context of the replication crisis.

Study designs

In a between-subjects design, each participant experiences only one condition. Different groups are compared. This avoids carry-over effects, where experiencing one condition changes how people respond to the next, but needs more participants, because differences between people add noise. In a within-subjects design, also called repeated measures, each participant experiences every condition, and each person serves as their own comparison. This needs fewer participants and is more sensitive, but introduces order effects: people get better with practice, get tired or bored, or learn about the robot in the first condition. Mixed designs combine both, for example comparing two robot designs between subjects while measuring each participant across three sessions.

Order effects in within-subjects designs are handled by counterbalancing: varying the order of conditions across participants so that each condition appears equally often in each position. With two conditions, half the participants get AB and half BA. With more conditions, complete counterbalancing becomes impractical (four conditions have 24 orders), so researchers use a Latin square, in which each condition appears once in each position, and a balanced Latin square, in which each condition also follows every other condition equally often.

Wizard of Oz studies deserve special mention. In them, a hidden human operator, the wizard, controls part or all of the robot's behaviour while participants believe it is autonomous. Laurel Riek's 2012 review of Wizard of Oz studies in HRI found that many papers reported little about the wizard's training, constraints or error rates, making results hard to interpret or replicate. Good practice is to script the wizard's options, train and measure wizard consistency, report the wizard's role clearly, and debrief participants about the deception afterwards. Video-based studies, in which participants watch recordings of robots, are cheap and scalable, but research comparing live and video presentation suggests that physical presence can change responses, so findings should be checked in live interaction before strong conclusions are drawn.

Participants and sampling

Many HRI studies recruit university students because they are convenient. Such samples tend to be young, educated and familiar with technology, and results may not generalize to older adults, workers, children or people with disabilities. Psychologists have criticized reliance on WEIRD samples (Western, educated, industrialized, rich and democratic) for drawing conclusions about humans in general. Studies should recruit participants who resemble the people who will actually use the robot, report demographics clearly, and avoid claiming more generality than the sample supports. Inclusion criteria, exclusion criteria and the recruitment method should be decided in advance.

Standard measures

Questionnaires should be validated: developed and tested to show they measure what they claim, reliably. Making up new items for each study makes results impossible to compare and of unknown quality. Three instruments are especially common in HRI.

The Godspeed questionnaire series, published by Christoph Bartneck, Dana Kulić, Elizabeth Croft and Susana Zoghbi in 2009, measures five concepts with semantic differential items, pairs of opposite adjectives rated on five-point scales: anthropomorphism (for example fake to natural), animacy (dead to alive), likeability (dislike to like), perceived intelligence (incompetent to competent) and perceived safety (anxious to relaxed). It is widely used and convenient, but later work has questioned some of its psychometric properties, such as overlap between scales, and the Robotic Social Attributes Scale, RoSAS, developed by Colleen Carpinella and colleagues in 2017, offers an alternative measuring warmth, competence and discomfort. Researchers should report reliability, such as Cronbach's alpha, for each scale in their own data.

The NASA-TLX, introduced in lesson 2, measures workload. The System Usability Scale, SUS, created by John Brooke in 1986 and published in 1996, is a ten-item questionnaire with five-point agreement scales, alternating positive statements (odd items, such as "I thought the system was easy to use") and negative statements (even items, such as "I found the system unnecessarily complex"). Its scoring converts responses to a 0 to 100 scale:

A SUS score is not a percentage. Benchmark data compiled by Jeff Sauro and James Lewis put the average across many products at about 68, so a score of 68 is roughly the 50th percentile, and scores above about 80 are in the top tenth or so. SUS is quick and robust even with small samples, but it measures perceived usability overall and does not diagnose specific problems, which needs observation and interviews.

# SUS scoring for a group and a comparison with the benchmark average of about 68
import numpy as np
rng = np.random.default_rng(430)
def sus(r):
    r = np.asarray(r)
    return 2.5 * ((r[:, 0::2] - 1).sum(axis=1) + (5 - r[:, 1::2]).sum(axis=1))
odd = np.clip(np.round(rng.normal(3.9, 0.7, (12, 5))), 1, 5)
even = np.clip(np.round(rng.normal(2.1, 0.7, (12, 5))), 1, 5)
resp = np.empty((12, 10)); resp[:, 0::2] = odd; resp[:, 1::2] = even
scores = sus(resp)
print("first participant responses:", resp[0].astype(int))
print("scores:", scores)
print(f"mean {scores.mean():.1f}, sd {scores.std(ddof=1):.1f}, share above 68: {np.mean(scores > 68):.0%}")

first participant responses: [5 2 4 1 5 3 4 2 3 1]
scores: [80.  70.  77.5 77.5 77.5 80.  72.5 65.  70.  80.  75.  77.5]
mean 75.2, sd 4.8, share above 68: 92%

Planning sample size

A study needs enough participants to detect the effect it is looking for. Statistical power is the probability that a study will detect an effect of a given size if it exists, usually set at 0.80 or higher at a significance level of 0.05. Effect size is often expressed as Cohen's \( d \), the difference in means divided by the standard deviation; values of about 0.2, 0.5 and 0.8 are conventionally called small, medium and large, though what counts as meaningful depends on the field. Many HRI studies have been underpowered, with samples of 10 to 30 participants that can only reliably detect large effects.

For a within-subjects comparison of two conditions analysed with a paired t-test, what matters is the effect size of the differences, \( d_z \), the mean difference divided by the standard deviation of the differences. If the standard deviation in each condition is \( \sigma \) and the correlation between a person's scores in the two conditions is \( \rho \), then \( d_z = d / \sqrt{2(1 - \rho)} \). A high correlation, common when people differ consistently from each other, makes within-subjects designs much more efficient. A normal approximation gives the number of participants:

# Power of a paired t-test by simulation, compared with the normal approximation
import numpy as np
rng = np.random.default_rng(430)
def power_sim(n, d=0.5, rho=0.6, reps=4000):
    cov = [[1, rho], [rho, 1]]
    null = []; alt = []
    for _ in range(reps):
        x = rng.multivariate_normal([0, 0], cov, n); diff = x[:, 1] - x[:, 0]
        null.append(diff.mean() / (diff.std(ddof=1) / np.sqrt(n)))
        y = rng.multivariate_normal([0, d], cov, n); diff = y[:, 1] - y[:, 0]
        alt.append(diff.mean() / (diff.std(ddof=1) / np.sqrt(n)))
    crit = np.quantile(np.abs(null), 0.95)              # two-sided 0.05 critical value
    return np.mean(np.abs(alt) > crit), crit
dz = 0.5 / np.sqrt(2 * (1 - 0.6))
n_approx = ((1.96 + 0.84) / dz) ** 2 + 1.96 ** 2 / 2
print(f"d_z = {dz:.3f}, approximate n = {n_approx:.1f}")
for n in (12, 20, 27, 35):
    p, c = power_sim(n)
    print(f"n = {n:2d}: simulated power {p:.2f} (critical |t| {c:.2f})")

d_z = 0.559, approximate n = 27.0
n = 12: simulated power 0.40 (critical |t| 2.24)
n = 20: simulated power 0.66 (critical |t| 2.05)
n = 27: simulated power 0.82 (critical |t| 2.04)
n = 35: simulated power 0.90 (critical |t| 2.02)

Research ethics review

Research involving people must be reviewed for ethics before it begins. HRI studies may seem harmless, but they can involve physical risk from robots, deception in Wizard of Oz designs, video recording of identifiable people, data from vulnerable groups such as children or people with dementia, and stress or embarrassment. Ethics review protects participants and researchers, and journals and conferences increasingly require authors to state that their studies were approved.

In Canada, research at institutions funded by the three federal research agencies, the Canadian Institutes of Health Research, the Natural Sciences and Engineering Research Council and the Social Sciences and Humanities Research Council, must follow the Tri-Council Policy Statement: Ethical Conduct for Research Involving Humans, known as TCPS 2, whose current edition is TCPS 2 (2022). It rests on three core principles: respect for persons, concern for welfare and justice. Studies are reviewed by a Research Ethics Board, or REB, with a proportionate approach in which minimal-risk studies may receive delegated review. TCPS 2 sets requirements for free, informed and ongoing consent, for privacy and confidentiality, and for research involving deception, which must be justified and normally followed by debriefing. It includes a chapter on research involving First Nations, Inuit and Métis peoples, requiring community engagement. The American counterpart is the Common Rule, 45 CFR 46, with review by Institutional Review Boards.

For an HRI study, the ethics application typically describes the robot and its safety measures, the risk assessment (lesson 4), recruitment, consent forms, any deception and debriefing, data handling and retention, video recording and its use in publications, and how participants can withdraw. Privacy law (lesson 11) also governs how personal information is collected and stored. Planning these details early often improves the study design itself.