When should an AI shopping assistant offer advice?

When piloting an assistant, compare paid orders and subsequent returns against a randomly assigned group without it. Make the purchase-quality decision after the return window, not when the chat ends.

Wang and colleagues (2025) randomized access to an assistant on an Asian livestream-selling platform. Their analysis covered 132,199 consumers. The reported increase was about 3% in orders placed, not three percentage points of visitor conversion or a universal revenue lift.

Among 35,164 consumers who placed orders, average product return rates were 4.015% without the assistant and 3.511% with it. The difference is 0.504 percentage points, or 12.55% lower relative to the control rate. This is a comparison of average consumer return rates, not a count of five fewer returned parcels per 1,000 visitors. The return regression was statistically clear at p < .05.

A completed checkout can conceal a poor match between customer and product. Following the transaction through returns makes that problem visible. Better pre-purchase answers are one plausible route to better decisions; an assistant should have to demonstrate that locally.

The returns comparison conditions on purchasing, which the treatment itself changed. The authors checked balance and matching, but this remains a material selection boundary. The randomized treatment was assistant availability in live shopping; it does not establish the same benefit on a static product page or prove that proactive prompts outperform customer-initiated help.

Test concise, task-relevant answers before adding jokes or unsolicited personal references. Let a stated question or a clearly expressed shopping need guide the response; do not treat urgency as permission to become more intrusive.

Zobair and colleagues (2026) report a U.S. retail field experiment with 409 participants, using transaction data, alongside 46 exploratory interviews. Personalized AI replies produced more purchases than humorous replies. The abstract describes competing helpfulness and intrusiveness pathways; urgency amplified both, while an existing retailer relationship softened intrusion.

The accessible primary abstract does not report purchase rates, an effect size or confidence interval. The sample counts do not supply those missing results. This supports a conditional response-style test, not a numerical sales target.

An answer earns attention when it helps with the task. A personal reference can also make the shopper wonder what the retailer knows and why it is using that knowledge. Those explanations motivate measuring helpfulness and discomfort separately.

The full result tables and exact intervention text were not accessible through the publisher and institutional searches. This is a directional extraction exception. The comparison was personalized versus humorous communication, not a randomized test of our suggested permission control or question-trigger rule.

Keep an accessible route to human help and test chatbot response across different shopping tasks. Treat shopper motivation as something to investigate, rather than assuming everyone welcomes automated advice.

Khan and colleagues (2024) compared chatbot and human product advice in online experiments. In Study 1, participants could spend a 50-cent bonus on one-cent lottery tickets for a tumbler. Mean ticket purchases were 5.49 after human advice versus 4.01 after chatbot advice: a difference of 1.48 tickets, equivalent to 1.48 cents of that bonus. This was a lottery decision, not an ordinary paid tumbler order.

The pattern also depended on motivational framing. In chatbot conditions, the mean was 5.34 tickets after a progress-and-aspiration message versus 2.58 after a safety-and-responsibility message. The interaction with assistant type was statistically clear (p = .02). This does not show that adding a cheerful slogan will raise store conversion.

Customers may approach the same interaction seeking exploration, enjoyment or reassurance. A single automated script may fit those tasks differently. The human route is our proposed safeguard for shoppers whose question remains unresolved; the paper did not test that control.

Study 1 reports 318 participants in its method text but 298 in its regression table; that inconsistency requires resolution. Study 2 used stated headphone purchase intention, not paid orders. These results cannot establish a percentage sales penalty for modern generative assistants or prove that a human handoff improves sales.

Before giving a product-specific answer, retrieve the relevant catalogue fact and show where it came from. If a decisive detail is uncertain, say so and provide a practical way to check it or ask a person.

A 2023 preprint by Spatharioti and colleagues tested vehicle-research tasks, not paid shopping. In its second experiment, 120 participants used the same language-model search tool. On a deliberately difficult comparison, correct choices were 26% with plain answers, 58% when high and low confidence were highlighted, and 53% when only low confidence was highlighted.

The two cue conditions were 32 and 27 percentage points above control: arithmetic equivalent to about 32 or 27 more correct decisions per 100 comparable task attempts, not extra purchases. The comparisons were statistically clear (p < .01 and p = .02). Even the better result left many decisions wrong.

A warning can prompt a shopper to check an answer before relying on it. A source link and a usable fallback make that check possible. These implementation choices are our inference, not the exact intervention tested in the paper.

This is supplementary preprint evidence, excluded from the peer-reviewed publication count. The tested cues used older models’ token probabilities, which are not calibrated probabilities that a fact is true. Do not copy their threshold into a production confidence score; the study does not validate modern systems, catalogue retrieval or our jacket example.