flowchart TB
subgraph F["Three recurring functions"]
A["Facilitator of<br/>individual expression"]
B["Decision-support<br/>tool"]
C["Market-intelligence<br/>source"]
end
E1["Era 1 (2000–2005)<br/>online communities;<br/>decision aids"] --> F
E2["Era 2 (2005–2010, ~50%)<br/>online WOM;<br/>support + intelligence merge"] --> F
E3["Era 3 (2011–2015, ~80%)<br/>expressive consumers;<br/>UGC as a tool"] --> F
13 Online Environments
Marketing now plays out in environments that are computer-mediated: search engines, social platforms, marketplaces, review sites, mobile apps, livestreams, and the augmented and artificially intelligent interfaces layered on top of them. These environments are not merely new channels through which old marketing flows. They change what consumers do, what firms can observe, and what researchers can measure. A consumer’s path to purchase is now studded with digital touchpoints that leave traces—clicks, queries, posts, ratings, dwell times—and those traces constitute a data stream of unprecedented granularity. The central premise of this chapter is that online environments are simultaneously a substantive domain (consumer and firm behavior changes online) and a methodological opportunity (the residue of that behavior is observable at scale).
The chapter is organized around the life cycle of digital marketing knowledge. We begin with how researchers collect data from online environments—application programming interfaces (APIs) and web scraping—and the validity threats and ethical constraints that attend them, because every empirical claim that follows depends on data gathered this way. We then trace the intellectual history of digital, social media, and mobile (DSMM) marketing, which supplies the organizing constructs for the rest of the chapter. The body proceeds channel by channel and mechanism by mechanism: email; social media and its functional anatomy; the firm-versus-user-generated content distinction; images as a data type; mobile and smartphones; online reviews and word of mouth; the e-marketplace and clickstream; search engines; livestreaming, augmented reality, and artificial intelligence as emerging interfaces; customer engagement; and the wisdom of crowds. By the end the reader should be able to situate a digital marketing phenomenon within the literature, identify the construct and the identification strategy a credible study of it requires, and reason about the data-collection and ethical constraints that bound what can be learned.
A note on scope and connective tissue. Online environments are where many constructs developed elsewhere in this book are now measured and contested. Brand image and brand-related online activity (@sec-branding) are increasingly inferred from images and posts; word-of-mouth and diffusion (@sec-innovation) are the engine of social platforms; advertising response (@sec-advertising) is estimated from clickstream and field experiments; and the marketing–finance link (@sec-marketing-finance) is tested by mapping social media metrics to firm value. This chapter is therefore best read as the empirical and environmental counterpart to those construct-focused chapters.
13.1 Collecting Data from Online Environments
Before any substantive claim can be made, data must be gathered—and online data are gathered in ways that introduce their own validity threats. Boegershausen et al. (2022) provide the methodological foundation: APIs and web scraping let researchers study genuinely new phenomena, raise the ecological validity of marketing research by observing behavior in situ rather than in the laboratory, advance methods for handling a new class of data, and improve measurement of constructs that were previously available only through self-report. The promise is real, but it is conditional on the data being collected and documented carefully.
13.1.1 Two Collection Modes: APIs and Scraping
An API is a sanctioned interface through which a platform returns structured data in response to programmatic requests; web scraping extracts data from rendered web pages that were designed for human consumption. APIs are cleaner and contractually safer but expose only what the platform chooses to expose; scraping can reach anything visible but is brittle, legally fraught, and ethically constrained. A firm rule follows directly: researchers should not create fake accounts to scrape data, because doing so violates platform terms and the norms of research ethics. The choice between modes is not merely technical—it determines the population the data represent and the inferences they will support.
13.1.2 Threats to Internal Validity
Online data are generated by systems that are themselves changing, and two threats to internal validity are endemic to them.
The first is algorithmic interference. The data a platform shows are filtered by sorting and recommendation systems, so what a researcher observes is the joint product of consumer behavior and an algorithm optimizing for the platform’s own objectives. Xu, Zhang, and Zhou (2019) demonstrate that ranking and recommendation algorithms confound observational inferences: an apparent effect of position or popularity may reflect the algorithm’s choices rather than consumer preference. Because the algorithm is typically unobserved and time-varying, it acts as a lurking variable that no amount of cross-sectional control can fully remove.
The second is inter-temporal instability. Data sources change—platforms alter their interfaces, fields appear and disappear, definitions drift—so a panel assembled over months may not measure the same construct at its endpoints. The practical consequence is that longitudinal online data require explicit documentation of when and how each variable was collected, lest a measurement artifact be mistaken for a substantive trend.
Following Gebru et al. (2021), researchers should treat data collection as a documented process, not an undocumented act. Three practices make online data research-grade: (i) a logbook that records important events during collection (outages, interface changes, sampling decisions); (ii) formal documentation of the collection process itself, in the spirit of “datasheets for datasets” (Gebru et al. 2021), so a reader can reconstruct what was gathered and why; and (iii) long-term archival of the data in a citable repository (Zenodo, Dataverse and the Harvard Dataverse, DataCite, re3data), released under a Creative Commons license where permissible so others can reuse it. These practices are the online analogue of a pre-registered protocol: they fix the chain of custody between the world and the dataset.
The substantive and technical challenges of computer-mediated research can be organized into three stages—data gathering (with its consumer-privacy and legal/ethical constraints on scraping), data analysis (feature extraction and dimensionality reduction on high-dimensional text, image, and behavioral data), and interpretation—and these stages frame the substantive challenges that recur below: sentiment-based and location-sensitive targeting, the rise of computers acting as consumers, and pervasive privacy risk (Yadav and Pavlou 2014).
13.3 Email
Email is the oldest digital direct-marketing channel and remains a clean testbed for personalization because messages can be randomized and outcomes (opens, clicks, purchases, unsubscribes) precisely logged. The evidence favors personalization, but the mechanism is subtle. Sahni, Wheeler, and Chintagunta (2018) find through field experiments that adding consumer-specific information—most simply, the recipient’s name—raises opening and sales and reduces the probability of unsubscribing, so personalization improves the contact rather than merely exploiting it. The effect generalizes beyond commerce: Munz, Jung, and Alter (2020) show that similarity between a donor and a donation recipient—a shared name, or even a shared first letter of the surname—encourages donors to open appeals and give more, evidence that the implicit-egotism mechanism behind name-based personalization operates in prosocial as well as commercial settings.
13.5 Who Generated the Content? Firm- versus User-Generated Content
A recurring fault line in digital marketing is who produced a piece of content, because source governs how it is processed and trusted. Firm-generated content (FGC) is controlled and polished but discounted for self-interest; user-generated content (UGC) is credible but uncontrolled. Colicev, Kumar, and O’Connor (2019) formalize the comparison through information processing and source credibility, mapping each type onto the marketing funnel: UGC correlates strongly with awareness and satisfaction, whereas FGC—especially its vividness—is more effective for consideration and purchase intent, with UGC valence dominating UGC volume at these stages. Brands with higher corporate reputation exhibit stronger relationships between FGC dimensions and the funnel, echoing the legitimacy logic of the OSM/ESM results above. The foundational observation that negative WOM behaves differently from positive WOM—both observationally and experimentally—predates this framework (Sen and Lerman 2007) and motivates the valence-centered measurement it uses. Figure 13.3 summarizes how the two content sources map onto the funnel stages.
flowchart LR UGC["User-generated content<br/>(credible, uncontrolled)"] --> AW[Awareness] UGC --> SAT[Satisfaction] FGC["Firm-generated content<br/>(controlled, discounted)"] --> CON[Consideration] FGC --> PI[Purchase intent]
A growing literature studies the hybrid and the responsive. Beck et al. (n.d.) examine firm-generated user content (FGUC)—brand-crafted content that consumers are encouraged to share—and find it increases sharing by lowering effort, but asymmetrically: satisfied consumers share it while dissatisfied consumers resist it because it misaligns with their experience, so FGUC amplifies positive WOM and suppresses negative WOM and should be deployed only when experiences are likely to be positive. On the firm’s reply, Saljoughian et al. (n.d.) build on dialogic-listening theory—empathetic understanding, unconditional positive regard, mutual understanding, presentness, and genuineness, plus shifting to private channels and signing replies with an agent’s name—and, analyzing roughly a million tweets across 206,000 threads at four US banks over a decade, show that specific response elements significantly improve subsequent user sentiment, with effectiveness contingent on the user’s prior sentiment. The managerial lesson is to match response tone and structure to initial sentiment rather than applying a uniform playbook.
The other party with a hand on UGC is the platform, whose blunt instrument is deletion. Whether removing a post improves what its author writes next is not obvious. Work on user bans points to psychological backlash, with users posting more but worse, while learning theory predicts the opposite: a removal is a cheap, specific signal of where the community’s line sits. Shan and Qiu (2026) test the two accounts on Reddit, using a difference-in-differences design across 40 communities; the university’s release puts the sample at about 10,000 users and more than 99,000 posts (UF Warrington College of Business 2026). Having a post removed reduced the author’s subsequent rule violations and raised the average upvotes on their later posts, the authors’ proxy for quality. The effects were stronger after repeated removals and when users saw peers’ posts removed, which the authors read as direct and vicarious learning; the release adds that explanations of why a post came down strengthened them further. The contrast with bans is the useful part for a platform-side marketer. A removal leaves the user free to keep posting, so the punishment arrives together with a chance to apply what was learned. Two caveats bound the result. Upvotes measure community approval, which tracks quality only insofar as the community’s taste does. And the quality outcomes can only be observed for users who post again; the abstracts do not say whether removal also changes how many users leave, which a platform would want to know before it treats deletion as training. (Only the published abstract was accessible when this section was written; the sample figures come from the release, and effect sizes are not reported here.)
13.5.1 The Platform as Author: AI-Generated Review Summaries
Deletion removes user content. A newer platform tool writes on top of it. Retailers including Amazon and Newegg now place a paragraph generated by a language model above the review list, condensing what reviewers say about a product (Z. Li et al. 2026). Most early work on these summaries looks at the reader. Z. Li et al. (2026) model two competing retailers on one platform and separate a convenience effect (reading the reviews gets cheaper) from a filtering effect (purchase decisions get better informed). The two push price competition in opposite directions, and the net effect depends on how far consumers trust the summary. On the empirical side, H. Wang and Wang (2025) track 3,781 Amazon products from February 2023 to February 2024 with a difference-in-differences design and find that the summary raised purchasing, more so for search than for experience products. Both studies take the supply of reviews as given. A summary might change that supply.
The intuitive prediction is crowding out. If a paragraph at the top of the page already says what the crowd thinks, the next customer has less reason to add to it. Q. Wang et al. (2026) find the opposite: introducing AI-generated summaries increased the volume of consumer reviews. Their mechanism is perceived collective efficacy. By presenting reviews as a collective force, the summary strengthens a customer’s belief that their own review contributes to a shared body of product knowledge. A controlled laboratory experiment measures perceived collective efficacy directly and finds that it mediates the effect of the summary on the likelihood of leaving a review. The field effect is larger for well-reviewed than for under-reviewed products, and for polarizing than for non-polarizing ones. The content changes too. After the summary appears, reviews are richer. Reviewers discuss fewer of the attributes the summary already covers and more of the attributes it leaves out. When they do discuss a covered attribute, they elaborate on it rather than restating the summary. Section 47.8 treats this covered/uncovered/elaborated coding as a measurement design.
The online appendix shows the field design and most of the estimates. The main field sample is Amazon’s Beauty & Personal Care department: about 3,000 products observed weekly (69,322 product-weeks), with the summary rolled out to products at different times. The headline two-way fixed-effects estimate on log(weekly reviews + 1) is 0.071 without controls and 0.060 with them. In levels, that is about 0.33 to 0.39 more reviews per product per week. The Callaway–Sant’Anna estimator, which avoids the forbidden comparisons of staggered timing (Section 44.5), gives 0.039 and 0.052. Three further comparisons make the result more than an Amazon-only pre/post contrast. The same products on Amazon’s US and UK storefronts are compared with product-by-storefront fixed effects. A kitchenware manufacturer’s weekly data for May–October 2023 compare products on Amazon, which had the summary, with the same products on Walmart, which did not (0.094). And the laboratory study shows participants a Newegg-style summary rather than Amazon’s. The moderators hold up as well. The extra effect for products with above-median pre-period review counts is 0.085, on a base effect of 0.020. For products with above-median rating variance it is 0.044, on a base of 0.048 (Q. Wang et al. 2026, Online Appendices A–E, L).
The appendix also qualifies the “complement, not repeat” reading of the abstract. In the US–UK sample, the number of reviews that mention a summary attribute rises (0.085), and so does the number that mention none (0.177). Reviews whose sentiment toward an attribute matches the summary’s tag rise (0.074), as do reviews that disagree with it (0.039). The laboratory comments show the same pattern. Among 80 participants per arm, 56% of treated versus 40% of control participants wrote a review mentioning a summary keyword, and 7.5% versus 1.25% wrote one mentioning none. By our arithmetic, that is about 64% versus 41% writing any review. The authors read this as two separate effects. Collective efficacy raises contribution overall, while complementarity shapes what the extra reviews say. It also tells against a pure “less redundancy” story, under which only gap-filling reviews should rise. Figure 13.4 lays out the argument.
flowchart LR S["AI-generated summary<br/>placed above the reviews"] --> E["Perceived collective<br/>efficacy"] E --> V["More reviews written"] S --> C["Review content:<br/>fewer covered attributes,<br/>more uncovered attributes,<br/>elaboration over restatement"] M["Stronger for well-reviewed<br/>and polarizing products"] -.-> V S --> R["Sales rank improves,<br/>more for top-ranked products"]
The two moderators locate the effect. A summary has more to say about a product with many reviews, so it is not surprising that well-reviewed products gain most. The cost is that the summary does little for the under-reviewed product, which is where one more review is worth most to a reader. A summary therefore does not solve the cold-start problem of thin review pages. The sales results point the same way. Weekly sales rank improves after the summary appears (log rank falls by 0.072). For products that were in the top 20% before the rollout it falls by a further 0.070, about twice the gain. The authors call this a Matthew effect: thin review pages give the model little to summarize, so the summary helps most where demand is already concentrated (Q. Wang et al. 2026, Online Appendix G). Average ratings of later reviews also rise, by about 0.11 to 0.12 stars. The polarization result connects to polarity self-selection (Schoenmueller, Netzer, and Stahl 2020). On a polarizing product the summary has to report a split, and one plausible reading (ours, not the authors’) is that a visible split makes one more voice feel consequential. The summary also inherits the limits of its inputs. In Section 13.8.4 most of the temperature effect sat in reviews that never mention the weather, so a summary generated from review text alone has nothing to correct with. It restates the contaminated consensus in more fluent prose. The appendix gives a partial look at what the summary draws on. The authors treat a pre-rollout review as “included” when it contains one of the attribute keywords Amazon lists under the summary, or a WordNet synonym of one. Whether a review was negative, written by an Amazon Vine reviewer, or recent does not predict inclusion. Longer reviews are more likely to be included, and reviews with a higher share of affective words are less likely. The summary therefore leans toward reviews written in a detailed, attribute-focused style. It does not lean toward a particular sentiment.
The comparison with the generative-AI shocks in Section 70.6 is instructive. When Stack Overflow banned ChatGPT answers, contributions fell (Borwankar et al. 2026), and when Lofter launched its own image generator, creator activity fell (H. Huang, Fu, and Ghose 2026). In both cases AI could substitute for the contributor’s own output. A review summary is built from that output, and on this evidence it draws more of it.
Three caveats apply. First, the collective-efficacy mechanism is established in the laboratory, in a 160-participant study built around wireless earbuds. Whether the field increase runs through the same channel, rather than, for example, through the summary making a product page look more active, is an inference from the pairing of the two studies. Second, a summary needs reviews to summarize, so a platform’s rollout could be selected on review momentum. The authors test this directly with a Cox hazard model of when each product received its summary. Review volume in each of the five preceding weeks does not predict the timing, although price and product tenure do. A shuffled-treatment placebo and an equivalence test on pre-period prediction errors also come out clean. Third, more reviews could simply mean more buyers, since the summary also lifts sales. The authors convert sales rank to estimated sales with a Pareto rank–sales curve. They calibrated its slope by buying 40 units of a near-zero-sales product and watching its rank move (\(\theta = 0.446\)). Reviews per estimated sale still rise. Because the denominator is itself estimated from rank, this check supports the propensity reading but does not settle it. (The main article was paywalled when this section was revised. The design details and estimates above come from the open online appendix, which reports the main estimates in its robustness tables. The text-measurement pipeline is described in Section 47.8.)
13.6 Images as a Data Type
Images are a high-dimensional, increasingly tractable data source for marketing, and a body of work now extracts marketing-relevant features from them with computer vision (connecting to brand image, @sec-branding). The competition for attention in such data-rich environments is fierce (Wedel and Kannan 2016), and even the design of feature ads can be optimized: Pieters, Wedel, and Zhang (2007) show that optimal allocation across brand, text, pictorial, price, and promotion elements is achievable without increased cost, and propose two entropy-based measures of clutter that characterize the salience of feature ads through attention-engagement theory.
13.6.1 Engineering a Score from Pixels
A representative pipeline scores the visual potential of an image from interpretable features. Structural complexity—visual complexity due to edges and detail (Pieters, Wedel, and Batra 2010)—is measured by Canny edge detection (Forsythe, Sheehy, and Sawey 2003), because edge information correlates highly with perceived complexity. Color complexity (Reinecke et al. 2013) is captured by a color-variety algorithm (Bing Zhou, Shuang Xu, and Xin-xin Yang 2015) that, for an image with \(m\) distinct colors, \(n_i\) pixels of color \(i\), and \(N\) pixels in total, computes the entropy-like quantity \[ C \;=\; \sum_{i=0}^{m} n_i \,\log\!\left(\frac{n_i}{N}\right), \tag{13.1}\] which rises with the number and balance of colors present. Image permanence—how well an image persists in memory after viewing—is scored by the AMNet memorability index (Khosla et al. 2012, 2015; Fajtl et al. 2018), validated to near-human consistency (Leyva and Sanchez 2021). The pipeline is completed by the number of faces (via a vision API), the aspect ratio (height over width), the average HSV values across pixels, and themes recovered by latent Dirichlet allocation over image labels. Each feature is interpretable and cheap to compute at scale, which is what makes image-based scoring practical.
13.6.2 What Visual Features Do to Engagement
The mapping from features to engagement is contingent on platform and category. Y. Li and Xie (2019) find a robust positive mere-presence effect of imagery on engagement and that high-quality, professionally shot pictures consistently raise engagement on both Twitter and Instagram, but that colorfulness matters only in some categories and that human faces and image–text fit raise engagement on Twitter but not on Instagram—so the value of a visual feature is platform-specific. Because that map is platform-specific and nonlinear, deciding which features to invest in is itself an optimization problem: Majumdar, Kumar, and Sriskandarajah (2026) separate the designer-controllable secondary features of a post (background detail, visual complexity) from its primary subject, estimate their nonlinear, platform-varying effect on engagement with deep learning, and show that allocating design effort by this estimated response beats common heuristics that budget by a platform’s audience size or ignore secondary features altogether—image analytics used to plan posts, not merely to explain them after the fact. For visual UGC, Jalali and Papatla (2016) operationalize color composition through hue, chroma, and brightness and find that click rates are higher for photos with more green and less red and cyan, and with higher chroma of red and blue. In the marketplace, professional imagery has measurable demand consequences: S. Zhang et al. (2022) use deep learning on 7,423 Airbnb properties over 16 months and find that verified, professionally photographed listings achieve 8.98% higher occupancy than host-photographed ones, with twelve composition-, color-, and figure-ground attributes significantly related to demand. Appearance also drives labor-market matching: Troncoso and Luo (2022) use computer vision and choice models on more than two million applications to 63,014 Freelancer.com jobs and show that freelancers who look the part are more likely to be hired regardless of actual performance, demographics, or attractiveness, with the effect strongest where reputation systems fail to differentiate candidates and only partially counteracted by platform recommendations.
13.7 Mobile and Smartphones
Mobile devices are not merely small screens; they are continuously present, deeply personal, and capable of new touchpoints in the customer journey. Rangone and Renga (2006) offer an early framework for mobile advertising. The strategic question of whether mobile investments create firm value is addressed by Boyd, Kannan, and Slotegraaf (2019), who use stock-market returns to show that announcing a branded mobile app raises firm value, and that the features emphasized in the app’s design—peer-to-peer interaction about the brand, personal brand–customer interaction, and the purchase phase—significantly shape how much value is created. Monetizing apps is harder than launching them: Cao, Chintagunta, and Li (2023) run a large-scale randomized field experiment on a non-advertising app and find that a “soft landing” (continued limited free access after monetization) and exclusive secondary offerings to subscribers each reduce willingness to subscribe in isolation, but interact positively when combined, because the soft landing reframes monetization as fair rather than aggressive—an interaction that generalizes in a follow-up experiment.
Smartphones also carry emotional weight. Melumad and Pham (2020) show that consumers derive not only functional but emotional benefits from their phones: under stress, consumers turn to their smartphones for greater stress relief, and this pacifying effect is stronger for one’s own phone than for another’s—evidence that the device functions as a personal attachment object, not merely a tool.
The device also has a persistent commercial puzzle attached to it. Smartphones carry most of the browsing and comparison traffic in retail yet convert at a substantially lower rate than PCs, and the usual explanations are frictional—small targets, fiddly checkout forms, interrupted attention. Yuen, Townsend, and Tsiros (2026) locate the gap somewhere less obvious: in what the device makes consumers believe about their own thinking. Across a series of studies they identify four characteristics of smartphones that lead consumers to feel they thought less thoroughly while using one, which lowers their perceived quality of the decision they just reached and, through that, their likelihood of buying. The finding that matters is the one that breaks the frictional account: objective decision performance on smartphones is equal to or better than on PCs, so the reluctance is not a rational response to a worse deliberation. It is a device-specific error in self-assessment—a metacognitive effect rather than a usability one—which is why the authors’ proposed remedies target perceived decision quality rather than the interface. For measurement this is the familiar warning in a new place: the operative variable is a second-order judgment about one’s own process (Chapter 39), and it is identified by the gap between it and the objective performance it is supposed to track, so a design that records only conversion cannot see the mechanism at all.
13.7.1 Push Notifications
The phone also lets a marketer interrupt. A push notification reaches the lock screen without the user opening the app, which makes it closer to direct mail than to a banner. Liu, Yang, and Kumar (2026) study 211 promotional campaigns on a U.S. mobile offer marketplace, with about 63 million user-campaign observations, of which about 4.1 million received a push. The platform chose recipients with its own affinity score, so recipients were already likelier to click. The main estimates are logit models that control for that score, with merchant and campaign fixed effects as robustness checks. Identification therefore rests on selection on observables. An instrumental-variable check in the online appendix uses the number of users each campaign targeted. Its first stage is adequate (\(F\) between 26 and 41), but the authors present it only as a complement, since a merchant’s reach may track its appeal.
The model’s predicted click-through rate is 1.05% with no pushes, 1.48% under the platform’s actual targeting and 6.64% if every user received one. The lift is largest for e-commerce, food and dining, and supermarket offers. Message design matters: urgency cues, emojis and deeper discounts strengthen the effect, and morning sends, iOS users and Fridays weaken it. A push also raises clicks on the same merchant’s other offers and, more weakly, on offers in other categories, both on the day and over the following week. Two online experiments test the limits. In the first, with about 1,000 participants, a push raised stated click likelihood from 3.94 to 4.94 on a seven-point scale. In the second, with 200 participants, repeated pushes drove click likelihood down from 4.41 to 3.80, below the no-push baseline of 3.86, while annoyance rose, and the median participant would accept one push a day. That is the repetition wear-out of Section 14.2 on a much shorter clock. The main text has not been read for this summary, which draws on the online appendix.
13.7.2 Recommending What Is Nearby
Location changes what a recommender is for. On a desktop, recommendations help a shopper search a large catalogue. On a phone, they narrow the choice to what is within walking distance. Han, Lee, and Kim (2026) study what happened to 16,720 restaurants in Seoul, Busan and Incheon when a Korean search engine launched a location-based recommender in April 2019. They follow each restaurant through a funnel from exposure (shown in a recommendation list) to click to visit intention (calling, saving or requesting directions). Their instrument, the launch combined with the number of rivals within the algorithm’s 400 m radius, is worked through in Section 44.6.3. A 1% increase in exposure raises clicks by about 0.078%, and a 1% increase in clicks raises visit intentions by about 0.053%. The second number rests on a weaker design.
The question for local business is who gains. Restaurants that are hard to reach, more than 30 m from a main road and more than 400 m from a subway or bus stop, gain more clicks from the same exposure, and the advantage holds through the first six months. But the extra clicks do not turn into extra visits. Conversion rises instead with the information a restaurant posts: reviews, photos, a menu and advertising all strengthen it, and they matter more for the hard-to-reach restaurants than for accessible ones. The algorithm can bring a back-street restaurant to a user’s attention, but the user still needs a reason to walk there. A restricted Seoul sample of credit-card sales also shows exposure moving with revenue, according to the abstract. The main text has not been read for this summary.
13.8 Online Reviews and Word of Mouth
Online reviews are the most studied online data type in marketing because they are abundant, structured (a rating plus text), and directly tied to sales. The literature can be organized around four questions: who writes reviews and how expertise shapes them; how text and emotion in reviews are processed; how reviews move sales across products and time; and how the integrity of the review ecosystem can fail.
One caution belongs at the front of that agenda. Treating a review corpus as a sensor reading understates what is happening inside it. Kozinets et al. (2010) followed a seeded blogger campaign ethnographically and found that participants did not simply transmit a message: they rewrote it to fit the narrative norms of their own community, so the same seed produced systematically different stories in different venues. Word of mouth is authored, not merely propagated, which is why a sentiment score computed across communities can average away the mechanism it is trying to measure.
13.8.1 Expertise, Emotion, and Helpfulness
Expertise systematically changes both the production and the effect of reviews. As people gain expertise they become more responsive to negative feedback—novices respond to positive feedback while experts seek and respond to negative feedback—a pattern robust across domains (Finkelstein and Fishbach 2012). Expertise also flattens evaluations: Nguyen et al. (2020) find that greater expertise yields less extreme evaluations and smaller effects on a brand-valence metric that affects page rank and consumer evaluation, so an excellent experience may earn a lower rating from an expert than from a novice, and observationally experts are more likely to post negative reviews. Emotional language is a separate lever: Folse et al. (2016) define negatively valenced emotional expression (intense language, all caps, exclamation points, emoticons) and show that such reviews are seen as more helpful and damage product attitudes when written by experts, but provoke a negative self-reflection and leave product attitudes unchanged when written by novices, with language complexity moderating the effect of expertise on trustworthiness.
The form of the text matters for measurement. Büschken and Allenby (2016) propose a sentence-based topic model for consumer reviews—rather than the usual word-based analysis—and show on hotel and restaurant data (Expedia, we8there) that sentence-based topics are more coherent and distinguished and improve inference and prediction of consumer ratings. Trust in reviews also depends on the type of purchase: Dai, Chan, and Mogilner (2019) show that reviews are less trusted for experiential than for material purchases, because ratings of experiences are less representative of objective quality; relatedly, X. (Shane). Wang et al. (2021) use machine learning and NLP to extract and monitor product attributes from review text, building embedded representations that characterize attributes by their surrounding words and cluster them into multi-level benefit abstractions, closing the gap between concrete engineered attributes and abstract meta-attributes that surveys capture inconsistently and slowly.
13.8.2 How Reviews Move Sales
The reviewer’s rank, the timing of reviews, and brand type all shape sales effects. Counterintuitively, Yazdani, Gopinath, and Carson (2018) find—using instrumental variables on 182 music albums and Amazon review data—that bottom-ranked reviewers move sales more than top-ranked reviewers, whose influence concentrates in new releases and in products with high review variability, with the disparity attributable to content and reviewer identity and robust across categories and metrics. The first review is especially fateful: Park, Shin, and Xie (2021) show that valence and volume are not independent and that a positive first review creates a long-term advantage in future WOM valence and volume while a negative first review imposes a long-term disadvantage, entrenched by information-availability bias that makes early negativity hard for firms to correct. Reviews of one product generation also spill onto another: L. Li, Gopinath, and Carson (2022) find that the valence of a previous generation’s reviews raises current-generation sales (amplified when current-generation reviews are uncertain or favorable) while current-generation valence depresses the previous generation’s sales.
Brand type moderates these effects. Hoskins et al. (2021), using US beer data, show that niche brands are more affected by online WOM because consumers hold weaker prior brand imagery, that reviewers favor local niche brands, that the online community’s sentiment outweighs professional critics’ for the average reviewer, and that prior reviews gain traction when the reviewer’s expertise is high or shares geography with the next reviewer. Identity-relevant brands are partially insulated: Ordabayeva, Cavanaugh, and Dahl (2022) show that negative reviews from socially distant (but not socially close) individuals are less harmful to identity-relevant brands, because a threat to an identity-relevant brand prompts consumers to strengthen their bond with it—an effect absent for positive reviews or irrelevant brands. Not all rating systems move sales: Nishijima, Rodrigues, and Souza (2021) find that Rotten Tomatoes’ “fresh”/“rotten” categorization has no effect on box-office performance.
All of these studies concern businesses already on a platform. The prior question is whether being listed at all matters, and it is not settled by default, because many businesses are not listed. Luca, Nagaraj, and Subramani (2026) match Texas mixed-beverage tax receipts to Yelp’s listing records and find that about 18% of alcohol-serving bars and restaurants still had no listing at the end of 2017, though a listing was free. Being added raised revenue by roughly 5% to 10%, including for 1,295 venues Yelp created in two days in 2010 from a purchased directory file. The venues that gain most are those that struggle to build a reputation otherwise (independents, tourist areas) and those with better products. The data source and its use are worked through in Section 33.8, and the paper’s argument is dissected in Section 76.6.4.
13.8.3 Herding, Polarity, and Sequencing
Reviews are not independent draws. Sunder, Kim, and Yorkston (2019) document substantial herding in online ratings driven by reference groups (the crowd and friends): as raters gain experience the crowd’s influence wanes while friends’ influence grows, divergent reference-group opinions produce varied herding, and a firm’s diverse product portfolio both raises perceived quality and dampens social influence on ratings. Schoenmueller, Netzer, and Stahl (2020) identify polarity self-selection—the people who post are disproportionately the very satisfied and the very dissatisfied—which reduces the informativeness of the average rating. Sequencing effects appear even between rating and tipping: Chen et al. (2022) show that when customers rate before tipping they tip less, because they feel they have already rewarded the provider through the rating, an effect stronger when they tip from their own pocket, have flexible categorization, or believe the provider benefits from ratings—and mitigated by highlighting the consistency motive between rating and tipping. The wording of the tip prompt matters too: on a freelance marketplace an injunctive-norm request (“It’s customary to leave a tip”) raised tipping more than reciprocity appeals did, with no detectable loss of repeat business (Kim, Amir, and Wilbur 2026); Section 20.6 works through that experiment and the wider tipping-culture debate. Q&A sections answered by other consumers and sellers improve product–consumer fit and reduce mismatch-driven negative reviews (Banerjee, Dellarocas, and Zervas 2021).
13.8.4 Context in the Rating: When the Weather Writes the Review
Herding and polarity are about who rates and in what order. A further distortion sits inside each rating. How a product feels in use depends on where and when it was used, as well as on the product itself, and raters do not separate the two well. Meister and Reinholtz (2026) show this with 218,913 REI ratings matched to local weather. Ratings of cold-weather gear (insulated and snow jackets, gloves and mittens, ski and snowboard clothing) rise with the temperature at the reviewer’s location in the days before the review, measured against that location’s normal for the season. Ratings of bicycles, tents, skis, and other products do not move with temperature. The effect is small per degree: 0.002 stars per degree Fahrenheit, or a standardized coefficient of .032. But it holds in 95% of 20,736 specifications, and the same pattern appears for rain jackets after rainy days. Section 54.6.2 covers how weather is matched to reviews and why the comparison identifies the effect. The scope of the effect is what separates the authors’ account from a mood story. If the weather on rating day lifted or lowered raters’ mood, every category would shift. Here only the products whose job is to keep people warm (or dry) move. The authors read this as misattribution: a cold day makes the wearer feel cold, and part of that feeling is charged to the jacket.
Three results matter for anyone who reads ratings as a quality signal.
- The text does not rescue the rating. GPT-4o mini coded 41.9% of the cold-weather reviews as mentioning the weather. Among those reviews, temperature had a small and nonsignificant effect on the rating (0.002, \(p = .171\)). Among reviews that did not mention it, the effect was 0.005 (\(p < .001\)). So the ratings most shaped by context are the ones that give a reader no hint of it. Whether a reviewer mentions the weather is not randomly assigned, however, so this comparison is suggestive. The experiments below supply the causal test.
- Small effects reorder short lists. The median REI product has six ratings, and 57.7% have fewer than ten. The authors re-rank the 30 top-rated men’s and women’s jackets after subtracting the estimated temperature effect from each rating. The correlation between the adjusted and raw rankings is .096 for men’s jackets and −.015 for women’s (.380 and .186 among the top 90). Across all jackets in a category the correlation stays above .97, so the reshuffling is local. But that local reordering is the part of the page consumers actually see, and position on the page drives search and purchase (Ursu 2018). Products used across a wider range of temperatures also have more dispersed ratings.
- Platforms can debias at the moment of rating, but only by naming the specific context and saying how it affected the experience. In Study 3, online participants read that they had used a product (a winter jacket, sunscreen, running shoes, a hotel bed, an energy drink, or a restaurant) and that their experience was either as expected or worse. The context (temperature, UV index, distance run, tiredness, hunger) was either absent, stated, or stated with an explicit note that it probably caused the experience. Each step toward awareness shrank the gap between good and bad experiences. In Study 4, a single winter-jacket scenario was rated after one of five rating prompts. Prompts asking raters to think about their context, even the weather specifically, barely helped. Prompts that explained how weather shapes warmth cut the experience effect by about 70%.
These findings add a third kind of noise to the review literature. The first two are self-selection into rating (Schoenmueller, Netzer, and Stahl 2020) and social influence across raters (Sunder, Kim, and Yorkston 2019; Park, Shin, and Xie 2021). Context noise arises inside the single honest rating. It also belongs with other evidence that inputs outside the product leak into product ratings. Late and early deliveries both lower rating valence (Nozari and Alavi 2026). The same Airbnb property earns lower ratings when it carries a “superhost” badge, because the badge raises expectations (Meister and Reinholtz 2025a). And consumers already discount ratings of experiences relative to material goods, because experiences are less representative of objective quality (Dai, Chan, and Mogilner 2019). For a platform, the practical point is that weather is observable even when the reviewer does not mention it. The same context data that contaminate a rating could be used to adjust it, or, less controversially, to recommend products that worked for raters in similar conditions.
The authors’ OSF archive (Meister and Reinholtz 2025b) posts data, code, materials, and preregistrations for the experiments. We re-ran Studies 3 and 4 from the posted files, and every published coefficient and \(t\) statistic is reproduced to three decimals (Table 13.1).
Code
ctx_tab <- data.frame(
Study = c(rep("Study 3", 4), rep("Study 4", 5)),
Term = c("Experience effect, no context information",
"x context stated (vs. absent)",
"x context stated and explained (vs. absent)",
"x context stated and explained (vs. stated)",
"Experience effect, baseline prompt",
"x 'consider your context' prompt",
"x 'consider the weather' prompt",
"x weather question + how weather affects warmth",
"x 'it was especially warm/cold' + how weather affects warmth"),
N = c(5306, 5306, 5306, 5306, 560, 560, 561, 573, 590),
Estimate = c(3.151, -1.019, -1.424, -0.404, 1.893, -0.285, -0.435, -1.307, -1.374),
SE = c(0.094, 0.127, 0.128, 0.122, 0.163, 0.237, 0.249, 0.238, 0.222),
t = c(33.577, -7.997, -11.162, -3.313, 11.585, -1.201, -1.748, -5.492, -6.189),
`Published t` = c(33.577, -7.997, -11.162, -3.313, 11.585, -1.201, -1.748, -5.492, -6.189),
check.names = FALSE)
knitr::kable(ctx_tab, digits = 3)| Study | Term | N | Estimate | SE | t | Published t |
|---|---|---|---|---|---|---|
| Study 3 | Experience effect, no context information | 5306 | 3.151 | 0.094 | 33.577 | 33.577 |
| Study 3 | x context stated (vs. absent) | 5306 | -1.019 | 0.127 | -7.997 | -7.997 |
| Study 3 | x context stated and explained (vs. absent) | 5306 | -1.424 | 0.128 | -11.162 | -11.162 |
| Study 3 | x context stated and explained (vs. stated) | 5306 | -0.404 | 0.122 | -3.313 | -3.313 |
| Study 4 | Experience effect, baseline prompt | 560 | 1.893 | 0.163 | 11.585 | 11.585 |
| Study 4 | x ‘consider your context’ prompt | 560 | -0.285 | 0.237 | -1.201 | -1.201 |
| Study 4 | x ‘consider the weather’ prompt | 561 | -0.435 | 0.249 | -1.748 | -1.748 |
| Study 4 | x weather question + how weather affects warmth | 573 | -1.307 | 0.238 | -5.492 | -5.492 |
| Study 4 | x ‘it was especially warm/cold’ + how weather affects warmth | 590 | -1.374 | 0.222 | -6.189 | -6.189 |
The two experiments agree on what works. Merely having the context available cuts the Study 3 gap by about a third (from 3.15 to 2.13 rating points). Adding the sentence “this was probably the reason” cuts it by almost half. In Study 4, every participant was told the weather, and the open-ended “consider your context” and “consider the weather” prompts did not reliably move ratings (\(p = .23\) and \(p = .08\)). Only the two prompts that explained how weather affects warmth worked. They reduced the experience effect from 1.89 points to 0.52 to 0.59. The authors stress the cost of this specificity: an effective prompt has to name the context that matters for the product, so no single prompt fits a whole catalog.
The full script reads the OSF files and is not run at render time.
Code
# Studies 3 and 4 of Meister & Reinholtz (2026, JM) from the public OSF archive
# (https://osf.io/vbax7/). Usage: Rscript mr2026_lab.R <path-to-OSF-download>
suppressPackageStartupMessages({library(data.table); library(lfe); library(car)})
args <- commandArgs(trailingOnly = TRUE)
osf <- if (length(args)) args[1] else "osf_vbax7"
lab <- file.path(osf, "Lab Studies")
coef_row <- function(study, term, fit, k) {
s <- summary(fit)$coefficients
data.table(study = study, term = term, n = nobs(fit),
est = s[k, 1], se = s[k, 2], t = s[k, 3], p = s[k, 4])
}
out <- list()
## ---- Study 3: 2 (experience, within) x 3 (awareness, between) x 6 products
data <- fread(file.path(lab, "Study 3.csv"))
data <- data[consent == "Next"]
dups <- data[duplicated(workerId)]$workerId
data <- data[!(workerId %in% dups)]
cat("Study 3 participants after exclusions:", nrow(data), "\n")
d3 <- melt.data.table(data, id.vars = c("workerId", "context"),
measure.vars = list(paste0("__js_goodbad_", 1:6), paste0("__js_product_", 1:6),
paste0("rating_", 1:6, "_1")),
value.name = c("experience", "product", "rating"))
d3 <- d3[!is.na(rating)]
d3[, badGood := ifelse(experience == "bad", -.5, .5)]
d3[, `:=`(absent = as.numeric(context == 0), light = as.numeric(context == 1),
heavy = as.numeric(context == 2))]
cat("Study 3 ratings:", nrow(d3), "\n")
# Awareness is between subjects, so its main effects are absorbed by the
# participant fixed effects; SEs clustered by participant (as in the paper).
f_abs <- felm(rating ~ badGood + badGood:light + badGood:heavy | workerId | 0 | workerId, data = d3)
f_lgt <- felm(rating ~ badGood + badGood:absent + badGood:heavy | workerId | 0 | workerId, data = d3)
out[[1]] <- coef_row("Study 3", "Experience effect, no context info", f_abs, "badGood")
out[[2]] <- coef_row("Study 3", "x light awareness (vs. absent)", f_abs, "badGood:light")
out[[3]] <- coef_row("Study 3", "x heavy awareness (vs. absent)", f_abs, "badGood:heavy")
out[[4]] <- coef_row("Study 3", "x heavy awareness (vs. light)", f_lgt, "badGood:heavy")
## ---- Study 4: 2 (experience) x 5 (rating prompt), between subjects, winter jacket
d4 <- fread(file.path(lab, "Study 4.csv"))
d4 <- d4[!is.na(rating_1_1) & attcheck_1 == "Winter Jacket"]
cat("Study 4 participants after exclusions:", nrow(d4), "\n")
d4[, rating := rating_1_1]
d4[, badGood := ifelse(experience == "bad", -.5, .5)]
lab4 <- c(none = "Baseline", context_general = "General", prime = "Weather",
expectation = "Expectations", explanation = "Explanation")
d4[, Prompt := factor(lab4[prompt_condition], levels = unname(lab4))]
omni <- Anova(aov(rating ~ experience * prompt_condition, data = d4), type = "III")
cat(sprintf("Study 4 omnibus experience x prompt: F(%d, %d) = %.3f\n",
omni["experience:prompt_condition", "Df"], omni["Residuals", "Df"],
omni["experience:prompt_condition", "F value"]))
b <- lm(rating ~ badGood * Prompt, data = droplevels(d4[Prompt %in% c("Baseline", "General")]))
out[[5]] <- coef_row("Study 4", "Experience effect, baseline prompt", b, "badGood")
for (pr in c("General", "Weather", "Expectations", "Explanation")) {
m <- lm(rating ~ badGood * Prompt, data = droplevels(d4[Prompt %in% c("Baseline", pr)]))
out[[length(out) + 1]] <- coef_row("Study 4", paste0("x ", pr, " prompt (vs. baseline)"),
m, paste0("badGood:Prompt", pr))
}
res <- rbindlist(out)
res[, `:=`(est = round(est, 3), se = round(se, 3), t = round(t, 3), p = signif(p, 3))]
print(res)
fwrite(res, "mr2026_lab_table.csv")Weather is not the only thing outside the product that ends up in a rating. Expectations do too. Rossi and Schleef (2026) compare MovieLens ratings of the same films in the 40 days before and after their Academy Award nominations, matching raters on taste vectors from a recommender trained on pre-nomination data. Matched users who rate after the nomination give about 0.04 fewer stars, and the drop is about three times larger on IMDb, where raters are less experienced. Review text points to disappointment and not to lost interest or contrarian reactions to a popular film. A quality signal that brings in viewers also raises the bar the film has to clear, so the average rating of a product falls just after it is certified. Section 4.4.1 works through the design.
13.8.5 The Afterlife of a Negative Review
The studies above treat a review as information that moves a purchase. Since Chevalier and Mayzlin (2006), the robust pattern in that literature is that negative reviews move sales more than positive ones do (see also Basuroy, Chatterjee, and Ravid 2003), one marketing instance of the broader finding that bad is stronger than good (Baumeister et al. 2001). Yadin et al. (2026) ask a question that sales data cannot answer: once the product has been bought, does a review read beforehand change the experience itself? Their answer is asymmetric assimilation. Negative reviews make the experience worse than it would have been with no reviews at all, while positive reviews leave it about where it would have been.
People do not expect this. In a pilot survey (N = 100), respondents predicted that reviews would push an experience in both directions and that positive reviews would have the larger effect. In Study 1 (N = 719, Prolific), participants listened to a higher- or lower-quality music clip after reading no reviews, negative reviews (a 2-star average plus five reviews), or positive reviews (a 4-star average). They gave the clip 2.91 stars after negative reviews, 3.33 after positive reviews, and 3.40 after none. Negative versus none was \(d = .463\); positive versus none was \(d = .067\) and not significant. Review valence did not interact with clip quality, so negative reviews dragged the experience down even when they contradicted what participants actually heard. Six supplementary studies (1a to 1f) carry the pattern to earbuds framed as utilitarian or hedonic, a book that was chosen or assigned, reviews whose wording was structurally matched across valence, a virtual tour rated after a short delay, a book rated after 24 hours, and an origami kit with extreme 1- and 5-star reviews. In every one, negative reviews lowered evaluations and positive reviews did not raise them. The effect reaches money: in a separate study (N = 599), willingness to pay for a ventriloquist show was $17.29 after negative reviews, $21.01 after positive reviews, and $20.45 after none.
The paper is worth reading as a ladder of designs, each rung closing a reading the previous rung left open (Table 13.2).
| Study | What is manipulated | Alternative it addresses | Key result (stars) |
|---|---|---|---|
| 1 (N = 719) | Review valence (none, negative, positive) x clip quality | Reviews merely matched true quality | Negative 2.91, positive 3.33, none 3.40; no interaction with quality |
| 2 (N = 999, prereg.) | When reviews are read: before choice, before consumption, between episodes, after consumption | Reviews change only what people report | None 3.41; read after consumption 2.87; read before 2.60 to 2.68 |
| 3 (N = 597, prereg.) | Majority valence x a fourth review of the same or opposite valence | Readers simply average what they read | One negative among positives 3.58 to 3.32; one positive among negatives 2.61 vs 2.60 |
| 4 (N = 376) | Review valence, then recall of five product attributes | Mechanism test | Share of recalled attributes disliked: negative .38, positive .27, none .22 |
| 5 (N = 1,600, prereg.) | Review valence x “form your own opinion” instruction | The effect is fixed once reviews are read | Negative 3.05 to 3.32 with the instruction; positive 3.78 vs 3.73 |
The timing study is the rung most worth copying. A lower rating after a negative review has two readings: the experience really was worse, or the experience was the same and the rater conformed to the crowd when writing it down. Reviews read after consumption but before rating can work only through the second channel, or through how the experience is remembered. In Study 2, reading reviews after consumption lowered ratings from 3.41 to 2.87, so conformity or reinterpretation is part of the story. Reading them at any point before consumption lowered ratings further, to between 2.60 and 2.68 (\(d \approx .21\) to \(.30\) against post-consumption reading). That further drop is the part that acts on the experience as it happens. The subtraction rests on an assumption worth stating: that the reporting component is the same whatever the timing. Because post-consumption reading can also rewrite memory (the backward assimilation of Oliver and Burke (1999), Chapter 4), the design cannot say how the post-consumption drop splits between reporting and remembering. Reading after choice but before consumption hurt as much as reading before choice, so having committed to the purchase gave no protection.
Study 3 shows the asymmetry in a mixed review set. One negative review among positive ones lowered ratings from 3.58 to 3.32 (\(p = .018\)); one positive review among negative ones did nothing (2.61 vs. 2.60). This is negativity dominance (Rozin and Royzman 2001): the combination is more negative than the parts would predict. The interaction itself was only marginal (\(p = .084\)), and the authors note that their analysis departs from the preregistered one, which they state is statistically equivalent. Both points belong in a reader’s assessment.
For mechanism, Study 4 asked participants to recall five attributes of what they had consumed. After negative reviews, .38 of recalled attributes were ones they disliked, against .27 after positive reviews and .22 after none. In a PROCESS Model 4 analysis the indirect effect on stars through this recall measure was \(b = .35\), 95% CI \([.167, .537]\), for none versus negative, and \(.24\), \([.060, .423]\), for positive versus negative. Study 4a, which measured recall before the evaluation, replicates the pattern, so the recall is not just a rationalization of a rating already given. Still, this is a measured-mediator design. Review valence is randomized, so its total effect is causal, but recall is not, and the step from recall to rating rests on sequential ignorability (Section 44.9.2). The indirect effect supports the selective-recall account; it does not prove it. Study 5 comes closer to an intervention on the process. Telling readers to “form your own opinion” raised ratings after negative reviews from 3.05 to 3.32 and left them unchanged after positive reviews (3.78 vs. 3.73; interaction \(F = 10.89\)). The authors also mention further studies, not reported in detail, in which the effect persisted when the reviews were framed as unreliable and whether they came from a friend or a stranger.
The result that matters most for the review ecosystem is the snowball. When Study 1 participants wrote their own reviews, text scored with the Evaluative Lexicon 2.0 (Rocklage, Rucker, and Nordgren 2018) was more negative after they had read negative reviews. A negative review therefore produces a worse experience, which produces a more negative review for the next reader. This gives a consumption-level mechanism for two field regularities above: herding in ratings (Sunder, Kim, and Yorkston 2019), usually read as social influence on what people report, and the long shadow of a negative first review (Park, Shin, and Xie 2021). Three limits apply. These are online experiments with short gaps between reading and consuming (the longest is 24 hours). Field shoppers who buy after reading negative reviews are a selected group, which the pre-choice condition of Study 2 only partly mimics. And the outcome is a stated rating, not repurchase. For practice, the authors argue that firms should treat negative reviews as a problem for customers who have already bought, not only for prospects, and that prompts to judge independently are a cheap remedy. Consumers, on this evidence, may be better off not reading reviews after they have bought. Data are posted on ResearchBox (3845) and the JMR Dataverse.
13.8.6 Valence Behind the Lens: Review Photos and Helpfulness
Reviews increasingly carry photos, and reviews with photos are judged more helpful, especially when the photo fits what the text says (Ceylan, Diehl, and Proserpio 2024), with effects that depend on the setting (Kübler et al. 2024). A separate, older regularity is that among reviews without photos, more negative reviews tend to be judged more helpful (Basuroy, Chatterjee, and Ravid 2003). Xue and Melumad (2026) put the two together. Their argument is that valence reaches the photograph: people who liked a product put more creative effort into photographing it, so photos attached to positive reviews have higher aesthetic quality, and better photos make a review feel more fluent and its author more trustworthy, which makes the review more helpful. The evidence comes from six studies with 4,218 lab and online participants and 669,937 field reviews.
The production side is established with two complementary designs. Study 1 (preregistered, N = 1,313 on Prolific) is within-subject: each participant reviewed an apparel item they liked and one they disliked. For liked items they reported more effort (4.65 vs. 4.18) and took more photos (2.12 vs. 1.95). Photo quality was scored three ways: by human judges (1,401 judges, 14,010 ratings; 3.56 vs. 3.29), by GPT-4o (3.97 vs. 3.82), and by the MUSIQ image-quality model (44.76 vs. 43.88, \(p = .019\)). In a structural equation model (lavaan) with the three quality scores as indicators of one latent quality, the indirect effect of valence through latent effort was \(b = .026\), 95% CI \([.006, .047]\). The within-subject design holds the reviewer constant, so photographic skill, phone camera, and personal taste cancel out. It does not hold the product constant, and products people like may simply be more photogenic.
Study 2 closes that gap. In the lab (N = 144), participants photographed cookies that looked identical, but one batch had been baked to taste bad. Appearance was fixed by construction, so any difference in the photos has to come from the photographer. Hidden cameras recorded the session (118 usable videos, 410 images). After a good cookie, participants reported more effort (4.10 vs. 2.88), took more photos (1.89 vs. 1.49), spent longer (19.88 vs. 13.70 seconds), and made more use of decorative props (4.64 vs. 2.97). Judges rated 58.9% of positive-review photos as well composed against 30.1% of negative-review photos, and 58.0% against 29.0% as pleasing. The indirect effect of valence on quality through effort was \(b = .433\), \([.297, .569]\). The cameras matter because a self-report of effort under a valence manipulation is open to demand and to justification (“I liked it, so I must have tried”); time and props are behavior.
The reader side follows. In Study 3a, 347 observers gave 1,735 ratings. Photos from positive reviews were rated higher in quality (4.25 vs. 3.73), with better lighting, color, and composition but no difference in visual complexity, and those photos were rated more helpful in conveying information about the product (5.40 vs. 5.14), through a serial path from quality to fluency and trust to helpfulness. Study 3b (preregistered) separates what a photo shows from how well it is taken. A 2 x 2 between-subjects design crossed the attractiveness of a shoe with whether its photo had been degraded (blur, exposure, and cropping applied in PowerPoint). Helpfulness was 4.89 for original photos and 3.52 for degraded ones (\(F = 155.67\)), with no main effect of shoe attractiveness and no interaction. Quality, attractiveness, and helpfulness were rated by separate samples, so the link between quality and helpfulness cannot come from one rater answering consistently across questions, which is the common-method problem of Chapter 3.
The field studies bring this to platforms: 348,108 Amazon reviews of 500 products (shoes, bags, hats; 24,996 with an image) and 321,829 Yelp reviews of 186 Los Angeles restaurants (82,472 with an image). Human judges again rated positive-review photos better: on Amazon, 72.3% vs. 39.7% well composed and 67.0% vs. 24.0% pleasing; on Yelp, 83.8% vs. 55.3% and 73.5% vs. 38.8%. Negative binomial regressions of helpful votes on the star rating, an image indicator, and their interaction show the consequence. On Amazon, the rating coefficient is \(-.143\), the classic pattern in which lower-rated reviews collect more helpful votes, but the image-by-rating interaction is \(.238\), larger in absolute value, so among reviews with images the pattern reverses. With product fixed effects the estimates are \(-.246\) and \(.314\), with the same conclusion. On Yelp the rating coefficient is \(-.240\) and the interaction \(.062\): the pattern is weakened, not reversed. The results hold with LIWC tone as the valence measure, with controls for review age, and in zero-inflated models. These regressions are observational (ratings and photos are not assigned), so the experiments carry the causal weight, and the field data show that the mechanism is large enough to matter where reviews are actually read.
The platform implication is direct. A platform that ranks reviews by helpful votes will tend to move positive reviews with photos up the page, not because they are more informative about the product but because their photos are better. Consumers who write negative reviews could do more for other shoppers by investing in their photos. And because the quality gap comes from motivation, not skill, the authors doubt that in-app photo-editing tools would close it. The three-way quality measurement is taken up as a measurement lesson in Section 49.4.2.1. Both papers report and justify their deviations from preregistration (here, a mixed model in place of the planned ANOVA), a habit worth copying.
Read together, the two papers show review valence shaping the review ecosystem, not just sales. Positive experiences produce better photos, which collect helpful votes and rise in the ranking. Negative reviews, once read, make experiences worse and seed more negative reviews. A regression of sales on average rating, the design behind Chevalier and Mayzlin (2006), folds both processes into one coefficient. Each paper also answers a “what else could it be” question with a design choice that transfers: holding the reviewer constant within subject, holding the product’s appearance constant by construction, observing behavior with hidden cameras, using separate rater samples, measuring one construct with several instruments, and manipulating timing to separate what people report from what they experience. Melumad’s earlier finding that the device used to write a review changes its content (Melumad, Inman, and Pham 2019) points the same way: the conditions under which user-generated content is produced are part of what it measures.
13.8.7 When the Review Ecosystem Fails
The credibility of reviews can be undermined from within. He, Hollenbeck, and Proserpio (2022) document a sizable market in which fake reviews are bought and sold (often through private Facebook groups): fake reviews raise ratings and sales in the short run, most large firms abstain, marketplaces struggle to police them promptly, and when firms stop buying fake reviews their ratings fall—driven by a rising share of one-star reviews— especially for young, low-quality products.
Review manipulation is easy to assert and hard to measure, because the manipulator is trying not to be measured. Two studies solved that problem in different ways and reached compatible but differently-actionable conclusions, and the contrast is a lesson in identification rather than in fraud.
2014 — identification by institutional asymmetry. Mayzlin, Dover, and Chevalier (2014) exploit a structural difference between two travel sites: one allowed anyone to post, the other only verified guests. Fake reviews should concentrate where posting is unverified, and the difference in a hotel’s rating across the two sites therefore identifies manipulation without ever labelling an individual review. The prediction that follows is about who: manipulation concentrates among independent hotels and those with a nearby competitor that stands to lose, rather than among chains with brand capital at risk.
2016 — identification by the platform’s own filter. Luca and Zervas (2016) use Yelp’s filtered-review data—reviews the platform itself flagged—and relate fraud to competitive conditions and reputational need. Restaurants are more likely to commit review fraud when their reputation is weak or when competition is intense.
Why the two designs matter more than the finding. Neither study asks a human to judge whether a review is fake. One infers manipulation from a difference between institutional regimes; the other uses a platform’s revealed classification and treats it as a measurement with its own error. Both are designs a marketing researcher can reuse whenever the behavior of interest is deliberately concealed: find a setting where the concealment technology differs across otherwise comparable units, and let the difference do the identification.
The practical reading is also consistent across them, and it is not “reviews are untrustworthy.” Manipulation concentrates where the incentive is strongest and the reputational stake is smallest—young firms, weak reputations, intense local competition—which is precisely where He, Hollenbeck, and Proserpio (2022) above find the practice and its unwinding. A rating should be discounted as a function of those observable conditions rather than uniformly.
The integrity question extends to whether review activity reflects genuine support: Sharma, Frake, and Watson (2025) exploit George Floyd’s murder as an exogenous shock and, using a difference-in-differences design on Yelp reviews and SafeGraph foot traffic, distinguish symbolic support (review frequency and sentiment) from substantive support (revenue and visits) for Black-owned businesses, finding a significant rise in symbolic support—especially from White and Democrat-leaning consumers—but no substantial rise in substantive support, plus more “not recommended” reviews suggestive of performative engagement.
13.8.8 Slacktivism
The Black-Lives-Matter results connect to slacktivism: supporting a political or social cause through social media or online petitions with minimal commitment. Silence, however, is not costless. Qin et al. (2024) study corporate silence on visible social issues (Blackout Tuesday) and find that staying silent significantly reduces consumer engagement—slower follower growth and fewer likes on Instagram—with peer activism amplifying the backlash to silence and narrow-market-niche firms facing less backlash than broad-market firms. The managerial implication is that firms must weigh issue salience, peer actions, and market positioning when deciding between silence and activism on contentious issues.
Whether a stance is followed by action is a separate question from whether it is taken at all. Chammas (2026) traces CEO activism—a CEO’s personal, public stance on a sociopolitical debate—from its drivers to its consequences across three essays. On the driver side, CEO narcissism emerges as a complement to the usual political ideology explanation, given its prevalence among CEOs and its link to attention seeking. On the consequence side, issue characteristics govern both the attention a stance attracts and whether the firm follows through with sustainability-related initiatives, and the issues most likely to draw attention to the CEO turn out to be the least likely to generate firm follow-through, even as they still travel into public and political debate and raise issue salience for policymakers. The symbolic-versus-substantive distinction from the Black-owned-business study therefore applies on the firm side as well: an executive’s stance and the firm’s action can diverge just as a consumer’s review and a consumer’s visit can.
The ideology explanation itself rests on a measure that deserves scrutiny, because executive ideology is usually read off political donations. Barber IV and Blake (2026) assemble executive donation records from 1980 to 2024 and treat executives as mixed-motive donors who give both expressively and strategically. Using non-executive donors as the counterfactual baseline of purely expressive giving, they show that bipartisan donations and donations to politically influential members of Congress mark strategic giving, that executives devote a larger share of their donations to it because of their role, and that the strategic share varies with compensation elasticity, firm size, political risk exposure, and whether the donor is the CEO. A donation-based ideology score therefore mixes a personal signal with a resource-dependence signal in proportions that differ across executives, which is a measurement problem in the sense of Chapter 3 before it is a theoretical one.
How far a stance travels also depends on who reports it. Iqbal, Pfarrer, and Gupta (2026) separate two stages of media coverage of corporate sociopolitical activism, whether an outlet covers a firm’s behavior at all and how it portrays it once covered, and argue that outlets balance an incentive to differentiate ideologically for readers against an incentive to stay credible for advertisers. Ideological congruence between the outlet’s orientation and the firm’s stance raises the probability of coverage but leaves the evaluative tone unchanged, a pattern the authors call bias allocation, with asymmetries between left- and right-leaning outlets in the supplemental analyses. For any study that measures activism’s reach through news volume, the selection therefore sits in the attention stage: the firms whose stances appear in a given outlet are those whose stances fit it.
Movements that never call for a boycott can still reach consumer spending, and they need not reach it evenly. C. P. Tran, Warren, and Beck (2026) trace #MeToo, which targeted sexual misconduct rather than any product, through the box office of 1,523 top-grossing U.S. films released between 2010 and 2023. Audiences penalized films featuring the behaviors the movement targeted. Their preferences for traditional gender roles held: they resisted counter-stereotypical portrayals of men and embraced counter-stereotypical portrayals of women only selectively (Chapter 28). The symbolic-versus-substantive distinction above therefore also runs through a single movement. The part of its message that names a wrong moved purchases. The part that proposes new roles did not, at least within the study window. A firm that reads a movement’s prominence as a uniform shift in demand will over-read it. Two of the same authors had earlier documented the investor side of this caution, finding that markets on average react negatively when firms take public sociopolitical stances (Bhagwat et al. 2020).
13.9 The e-Marketplace and Clickstream
The e-marketplace is where browsing and buying are jointly observed, and clickstream data—the sequence of pages a user views—make the path to purchase visible. Early descriptive work established the terrain: Dholakia and Rego (1998) document the marketing information on commercial home pages and the factors that drive hit rates, drawing on the information-content paradigm to assess informativeness, while Burke (2002) surveys 2,120 consumers across 128 facets of shopping and finds general satisfaction with convenience, quality, selection, and value but dissatisfaction with service, product information, and speed, concluding that new interface technologies help when customized to consumer segments and product categories. Shoppers are heterogeneous: Rohm and Swaminathan (2004) segment them by shopping motive (convenience, store orientation, information use, variety seeking) into convenience shoppers, variety seekers, balanced buyers, and store-oriented shoppers.
13.9.1 Who Adopts the Online Channel, and Why
Segmenting shoppers by motive, as Rohm and Swaminathan (2004) do, raises a companion question that transaction data can answer directly: what moved a given customer online in the first place? S. Biswas, Yoganarasimhan, and Zhang (2026) show that the answer is a first-order predictor of what happens next. Tracking previously offline-only customers of a large Brazilian retailer over 63 months, they compare adoption triggered by a macro shock (the March–April 2020 lockdown), by a one-day Black Friday promotion, and by a loyalty-program launch against adoption that happened organically. Every group spends more than comparable offline-only customers—the standard multichannel result—but the groups diverge sharply from each other. Shock-induced adopters keep about 7 percentage points more of their spending offline than organic adopters, a gap concentrated among older customers and consistent with habit persistence; promotion-induced adopters spend 9–14% less than organic adopters after the event, with the spike-then-dip pattern of forward buying.
For research design, the lesson is that “adopted the online channel” is not a treatment but a bundle of treatments with different selection mechanisms attached, and that the comparison group implied by “customers who did this before” typically encodes a readiness the firm’s promotion does not buy. Section 16.8 develops the value consequences.
The arrival of broadband is the same question at the scale of a whole market. Over broadband’s spread from 2004 to 2019, U. Tran (2026) finds modest average effects on how households bought consumer packaged goods, with sharp declines in brick-and-mortar shopping among younger consumers and stability among the larger older cohorts, an age gradient like the one above. Raj (2026) finds that, in 1999–2008, before online retail was a serious competitor, broadband availability made physical retailers less likely to exit, which Raj attributes to lower consumer search costs. The designs these and other broadband studies use are compared in Section 44.6.6.
13.9.2 Opening Stores for an Online-First Retailer: Halo or Cannibalization?
When a retailer that began online opens physical stores, two stories compete. In the halo story, the store advertises the retailer, lets shoppers handle the product, and lifts online sales around it. In the cannibalization story, the store mostly serves customers who would have bought on the website anyway. The early evidence leaned toward the halo. Bell, Gallino, and Moreno (2018) find that showrooms opened by an online-first eyewear brand raised demand both overall and in the online channel, with operational benefits such as fewer returns. K. Wang and Goldfarb (2017) show that the answer depends on where the store opens: online sales and search rise after an opening where the retailer’s presence was weak and fall where it was already strong. Avery et al. (2012) add that a store’s effect on a retailer’s catalog and online channels changes with time since opening.
Çetinel, Kök, and Rooderkerk (2026) revisit the question with a different kind of retailer, a leading multi-brand consumer-electronics retailer in Western Europe that began online and by 2019 sold through a website, an app and 11 stores in two neighbouring countries. Three stores opened that year in two formats. The two large stores (about 800 m²) were experience-centric, with up to 65 products per category on display in a minimalist layout and inventory kept in the back. The small store (about 110 m²) was convenience-centric, with up to 20 products in its top categories and no large items such as televisions or washing machines. With monthly zipcode-level sales from January 2018 to February 2020, which stops before COVID-19, the authors treat zipcodes within a 20-minute travel time of a new store as exposed, match them to unexposed zipcodes, and estimate a staggered event-study difference-in-differences. Section 44.5.1 covers the design. The numbers below come from the April 2026 working-paper version (Çetinel, Kök, and Rooderkerk 2025), with confidence intervals in brackets.
In the opening month and the three months after it, net revenue from exposed zipcodes rose 21.7% [11.3, 32.1] around the first large store and 23.2% [15.4, 31.1] around the second. The small store produced no measurable growth. The gain came from more orders rather than higher prices or larger baskets, and from both new and existing customers. The first large store, the only one observed long enough, was still adding 27.5% [16.5, 38.4] in the later bin. Online net revenue, however, fell in the short term: −7.8% [−15.5, 0.03] around the first large store, −10.5% [−16.6, −4.4] around the second and −9.8% [−17.4, −2.2] around the small store. There was no halo. The stores added revenue in total while taking some of it from the retailer’s own website, and the online loss was significant only for zipcodes within ten minutes of a store.
The small store’s failure could reflect what it stocked rather than how it sold, since it carried fewer and smaller categories. The authors check this by restricting the outcome to categories that both formats carry. The large stores still grow 22.5% and 23.8%, and the small store’s +6.9% is not significant. The difference between formats is the experience, not the assortment. Within the large stores, the effect is far from uniform across categories. Desktops, televisions, earbuds and mobile phones more than doubled, while more than 40% of categories, among them printers, washing machines and electric toothbrushes, showed no significant uplift.
The contrast with Bell, Gallino, and Moreno (2018) says more about the retailer than about the method. A single-brand digital native that opens a showroom is also introducing its brand to the neighbourhood. A multi-brand retailer selling products that shoppers can buy in many places has less of that work left for a store to do, which is closer to the strong-presence condition under which K. Wang and Goldfarb (2017) find substitution. That reading is ours, not a test in either paper, but it suggests how to report such studies. The retailer’s type, the store format and the distance gradient are scope conditions for any halo or cannibalization estimate, and a finding from one cell of that grid should not be applied to the others.
13.9.3 Modeling Browsing Paths
Clickstream models turn navigation into prediction. Montgomery et al. (2004) propose a dynamic multinomial probit model of web browsing on data from an online bookseller and show that a memory component is essential: the dynamic model predicts paths far better than static multinomial probit or first-order Markov models, because a user’s path reveals their goal. Practically, purchasers can be predicted with over 40% accuracy after only six page views, against a 7% base rate—evidence that path data personalize web design and product suggestions. The browsing literature complements this with individual-level models: Bucklin and Sismeiro (2003) model browsing from clickstream and show that the propensity to browse depends on visit depth and repeat visits and that aggregate site metrics cannot capture individual behavior. Context matters too: Mallapragada, Chandukala, and Liu (2016) use a multivariate mixed-effects Type II Tobit model on 773,262 sessions yielding 9,664 transactions across 43 categories and 385 sites, finding that a site’s product-variety breadth raises visit length and basket value but lowers page views, and that communication functionality raises basket value especially for hedonic products.
13.9.4 Real-Time Adaptation and Cross-Selling
The frontier is acting on observed intent in real time. Ding, Li, and Chatterjee (2015) develop a dynamic model that learns a shopper’s unobserved real-time intent from cart actions and instantly adapts the web page, lowering cart abandonment by 32.4% and raising conversion by 6.9% when adaptation begins after the first page view, with the most efficient intervention point after three page views—balancing learning against timeliness. Sequential structure also organizes cross-selling. S. Li, Sun, and Wilcox (2005) use a structural multivariate probit model on bank data to show that customers buy products in a natural order along a financial-maturity continuum, with women and older customers more influenced by overall satisfaction and more-educated or male-led households progressing faster. S. Li, Sun, and Montgomery (2011) extend this with a stochastic dynamic programming framework that delivers the right product to the right customer at the right time through the right channel: cross-selling solicitations serve mainly an educational role (83%) rather than advertising (15%) or immediate promotion (2%), and the optimized policy raises immediate response 56%, long-term response 149%, and long-term profitability 177%.
13.9.6 Peer-to-Peer Platforms
Platform business models reshape how consumers reason about purchases. Costello and Reczek (2020) show that peer-to-peer (P2P) platforms (Uber, Lyft, Airbnb) mediating flows between providers and consumers can shift buyers into an “empathy lens”— thinking about how a purchase affects the provider—rather than the “exchange lens” of money-for-service with a firm, raising purchase-related outcomes when the platform foregrounds providers, a pattern confirmed across field and lab studies and absent in traditional business models.
13.10 Search Engines
Search is where demand is expressed as a query, and the structure of the search-results page shapes behavior. Attention concentrates at the top: Guan and Cutrell (2007) document the “golden triangle,” in which users attend to the top three organic results and spill over to the fourth (often paid). Search behavior is shallow and slow-moving: E. J. Johnson et al. (2004), using panel data on more than 10,000 households across books, CDs, and air travel, find that households visit only about 1.2 book, 1.3 CD, and 1.8 travel sites per active month, that search follows a logarithmic process with limited breadth, and that more-active shoppers search more sites. Search data are also predictive of demand before it materializes: Kulkarni, Kannan, and Moe (2012) show that pre-launch search volume forecasts opening-week motion-picture sales, with advertising data improving the forecast—turning queries into a leading indicator for launch planning.
The design of search aids is a fertile field-experimental domain. Lei, Chen, and Sen (2024) show that firms leveraging an external autocomplete API gain measurably: removing access cut search-suggestion clickthrough rate (CTR) by 4.6%, and an instrumental-variables analysis establishes that a 10% change in suggestion CTR causes a 1.85% change in top-slot results’ CTR, with the negative effect of losing external data halving over the long run as firms accumulate internal data—a strategic trade-off between external data as growth instrument and as constraint on internal capability. Query recommender systems likewise expand demand: Zheng et al. (2023) find that access to a query recommender on an Asian food-delivery app raises 30-day purchase volume by 1–2% and broadens consumption diversity, working in complement with autocomplete by expanding consideration sets while autocomplete refines queries. Finally, sponsored search can cannibalize organic traffic: Moshary (2025) block sponsored ads for 3% of a platform’s visitors and find that sponsored search reduces total transactions yet remains profitable, because ad revenue more than offsets lost commission—so what harms total market efficiency can still be a net financial positive for the platform.
13.10.1 Generative Search and the Customer Journey
Every search aid above starts from a query the consumer has already typed: autocomplete finishes it, and a query recommender suggests the next one. Generative search steps in earlier. It puts an AI-generated response above the conventional results and lets the consumer describe what they need in ordinary language rather than in keywords. Zheng et al. (2026) frame what this changes. Keyword search makes the consumer translate an underlying need into an effective query before the search engine sees anything, so the mapping from problem formulation to keyword articulation has always happened privately and has never been observed. Generative search moves the interaction upstream to the formulation stage and makes it observable for the first time. The authors test whether this helps commerce with a large-scale field experiment on Meituan, a leading Chinese technology platform, the same kind of setting in which Zheng et al. (2023) evaluated a query recommender. (Only the published abstract was accessible when this section was written. The directional findings below are the authors’; their effect sizes are not reported here.)
Generative search significantly increases consumer purchases. The behavioral evidence shows where in the journey the gain comes from. Consumers who see the AI answer go on to issue more effective and more diverse keyword queries, do less exploratory browsing and clicking, and concentrate their evaluation within relevant categories and merchants. The explanation the authors find most consistent with the evidence is informational. The AI answer tells consumers something about their own underlying need, widens their awareness of the attributes that matter, and shifts their attention toward the relevant categories. In other words, it performs part of the exploration that browsing used to perform. Figure 13.5 sets this route beside keyword search and beside a third route: a general-purpose assistant off the platform that refers the consumer onward, the channel documented in Section 13.11.
flowchart TB
N["Underlying need<br/>or problem"]
N -.->|"formulated privately,<br/>translated into keywords"| KW
N -->|"stated in natural language<br/>to the platform"| GS
N -.->|"stated to a general-purpose<br/>AI assistant"| AS
subgraph KW["Keyword search"]
direction TB
K1["Keyword query:<br/>first thing the<br/>platform sees"] --> K2["Ranked results"]
K2 --> K3["Exploratory browsing<br/>and clicking across<br/>categories and merchants"]
K3 --> K4["Evaluation<br/>and purchase"]
end
subgraph GS["Generative search"]
direction TB
G1["Intent in natural<br/>language, now observed"] --> G2["AI answer before results:<br/>clarifies the need, surfaces<br/>attributes, points to categories"]
G2 --> G3["More effective and<br/>more diverse<br/>keyword queries"]
G3 --> G4["Less exploratory browsing;<br/>evaluation within relevant<br/>categories and merchants"]
G4 --> G5["More purchases"]
end
subgraph AS["Off-platform AI assistant"]
direction TB
A1["Conversation the<br/>retailer never sees"] -.-> A2["Answer with an<br/>outbound link"]
A2 -.-> A3["Referral visit lands<br/>on the retailer's site"]
A3 --> A4["Engaged visitors, but<br/>conversion below organic<br/>search; gap smaller in<br/>complex categories"]
end
Read across the three columns, the figure shows three ways AI is changing the journey. First, the earliest observed moment moves upstream. A platform running generative search records a statement of need rather than a query, which is data on a stage of search that used to be invisible. The authors draw this implication themselves, calling for search models that begin at the intention-expressing stage rather than at the query. Second, the middle of the journey compresses. If the answer does part of the exploring, fewer clicks precede a purchase, so browsing depth and click counts stop being clean engagement metrics. In this experiment, less clicking came with more buying, and a dashboard that read the fall in clicks as lost engagement would get the sign of the effect wrong. Third, where the AI sits determines who sees the journey. Built into the platform, it gives the seller a view of the need itself; run by a general-purpose assistant off the platform, it takes formulation and advice out of the seller’s sight, and the first observed touchpoint becomes a referral visit (Kaiser and Schulze 2026). The same technology extends a firm’s view of the customer journey in one case and shortens it in the other. The difference matters for the attribution models of Chapter 36, which can credit only the touchpoints that appear in the data.
13.11 Emerging Interfaces: Livestreaming, Augmented Reality, and AI
Three interface technologies are reshaping how consumers encounter products, each introducing a distinct psychological mechanism.
Livestreaming fuses entertainment, social presence, and commerce in real time. Lin, Yao, and Chen (2021) show that happy streamers make audiences happier and more generous with tips, an effect amplified for broadcasters who are more experienced, receive more tips, and are more popular—evidence that emotional contagion is a monetizable mechanism. Emotional display does not always help in screen-mediated selling, however: Bharadwaj et al. (2021) extract salesperson emotions from livestream video and find that in one-to-many screen-mediated communication salespeople should not display emotions, a contingency that cautions against importing face-to-face selling norms wholesale.
Studies of livestreaming have mostly looked at the live stage. A stream also has an afterlife as a recording, and the two stages can sell to different people. Cong, Liu, and Manchanda (2026) find that on a Chinese paid-livestream platform, where the recording sells at the same price as the live ticket, demand before the stream is more price-sensitive than demand for the recording. Early buyers tend to be the platform’s heavy users, and quality is uncertain until ratings arrive after the stream. The pricing consequences are in Section 21.8.2.
Augmented reality (AR) overlays digital content on the physical world. Yim, Chu, and Sauer (2017) show that, relative to web-based product presentation, AR delivers superior communication benefits—novelty, immersion, enjoyment, utility—leading to better medium attitudes and purchase intention, with immersion mediating the path from interactivity and vividness to usefulness and enjoyment in the AR condition but not on the web. The construct of vividness, “the ability of a technology to produce a sensorially rich mediated environment” (Steuer 1992, 80), and the two schools of interactivity (a technological view emphasizing speed, mapping, and range; and a subjective-perception view tied to motivation) are the theoretical scaffolding here, and their overlap is a measurement challenge the literature continues to negotiate.
Artificial intelligence introduces agents that consumers reason about differently from humans. Garvey, Kim, and Duhachek (2021) show that consumers respond better to an AI agent than a human when an offer is worse than expected, and better to a human when an offer is better than expected, because AI agents are perceived to have weaker intentions; firms can anthropomorphize AI to claim credit for good offers and deflect blame for bad ones. The visual perception of AI-rendered and animated content also has its own biases: Jia, Kim, and Ge (2020) document an inverse size–speed association in digital ads—faster animation makes an object seem smaller, learned from animate agents such as animals— which firms can mitigate by reducing similarity to those domains, educating consumers, or highlighting size information, and which can even reverse when a positive size–speed association in the base domain is made accessible. A broader typology of digital agents is offered by Miao et al. (2021), who define avatars as “digital entities with anthropomorphic appearance, controlled by a human or software, that are able to interact” (p. 5) and organize them on form realism and behavioral realism. Even the platform on which content is consumed conditions preferences: KOUKOVA, KANNAN, and RATCHFORD (2008) find experimentally that content-consumption preferences (e-book versus print, and so on) vary across platforms.
Artificial intelligence is also becoming a channel, not merely an agent consumers reason about. When a conversational assistant answers a shopping question and links out to a retailer, it refers commerce traffic much as search engines and affiliates do—a channel that did not exist before August 2024, when ChatGPT began emitting organic outbound links. Kaiser and Schulze (2026) document it across 973 e-commerce sites in that first year: organic LLM referrals convert below every traditional channel except paid social (roughly 13% below organic search and 86% below affiliate) and earn less per session, yet their visitors are unusually engaged, the shortfall shrinks in complex product categories where an assistant’s guidance is worth more, and both conversion and revenue per session climbed steadily across the year. The lesson is not that assistants rival search today—they still carry under 0.2% of visits—but that a genuinely new organic channel has appeared and is maturing, one no advertiser bids into.
13.12 Customer Engagement
Engagement reframes the customer as more than a buyer. Kumar et al. (2010) decompose a customer’s engagement value into four components: customer lifetime value (purchase behavior), customer referral value (incentivized referrals), customer influencer value (organic influence on other customers), and customer knowledge value (the value of the customer’s feedback to the firm). Harmeling et al. (2016) visualize the mechanism by which engagement translates into firm performance, completing the conceptual bridge from behavior to value. Engagement is heterogeneous and observable in clickstream: Bucklin and Sismeiro (2003) show that browsing propensity varies with site-visit depth and repeat visits, and Reimer, Rutz, and Pauwels (2014) show that segments respond differently to marketing instruments—heavy users of digital music are less price-sensitive and more responsive to TV advertising than the consumer-packaged-goods pattern would predict, while light users are price-sensitive and prone to opt out of targeted communication. The lesson is that engagement-based segmentation must be estimated, not assumed.
13.13 The Wisdom of Crowds
Online environments enable production and evaluation by distributed crowds—open source, crowdsourcing, and crowdfunding—whose success turns on network structure and social dynamics rather than on a single firm’s effort.
In open source, network embeddedness is double-edged. R. Grewal, Lilien, and Mallapragada (2006) apply latent-class regression to affiliation networks of open source projects and find that embeddedness profoundly shapes technical and commercial outcomes, but heterogeneously: in some regimes it promotes success and in others it harms it, with project age and visibility offering additional explanation. Mallapragada, Grewal, and Lilien (2012) model time-to-release with a split-hazard model on 817 SourceForge projects and show that a founder’s central position in the developer-user community can speed release by up to 31% and that highly engaged end users cut release time by 11%, confirming the dual-community (developer/end-user) structure of open source. In crowdsourcing, Mahr, Rindfleisch, and J Slotegraaf (2015) apply dual-processing theory and find that creative (spontaneous, intuitive) and deliberate (systematic, analytical) problem-solving styles each succeed under different conditions—creative under high contextual familiarity and short time investment, deliberate under low familiarity and long investment—while combining both styles lowers success.
In crowdfunding, social affiliation can backfire. Herd, Mallapragada, and Narayan (2022) find that while more backers raise funding, affiliation among backers lowers funding amounts and success through “vicarious moral licensing”—potential backers feel less obligated when affiliated others have already funded—an effect attenuated by creator engagement (descriptions, updates) and backer engagement (shares) and robust across instruments, models, and measures.
Donation-based crowdfunding, in which contributors receive nothing in return, raises a further question: not only whether a campaign succeeds but who gets funded. Person-to-person crowdfunding has become an increasingly important form of disaster relief, and it is promoted as a way to connect people in need with anyone able to help. Cookson, Gallagher, and Mulder (2026) test that promise after Colorado’s Marshall Fire of December 2021. They link the GoFundMe campaigns raised for households whose homes burned to property records and to household credit files, which lets them compare households that lost similar property but entered the fire with different finances. Holding property losses constant, higher-income households were 12 percentage points more likely to have a campaign at all and raised over 25% more. The authors trace the gap to unequal social capital rather than to need: higher-income households had broader donor bases, more ties outside the local area, more advocacy by friends who organized campaigns for them, and more generous donors. They also report that donors in online crowdfunding appear to respond to social pressure. The working-paper version gives the scale and a decomposition (Cookson, Gallagher, and Mulder 2024). Campaigns naming an individual or household raised $23.15 million, against uninsured losses that the state insurance regulator put at $86 million to $155 million and just over $2 million in direct FEMA grants to individuals. In that version, a 10% higher income brought about six more donations, enough by the authors’ calculation to explain most of the income gradient in proceeds, while larger average gifts accounted for about 40% of it. (The published article was not accessible when this section was written. The 12-point and 25% figures come from its abstract, and the decomposition comes from the January 2024 working paper, whose headline estimates differ somewhat.)
Three lessons carry over to research on online environments. First, removing the intermediary does not remove the network. A campaign page reaches donors through the beneficiary’s existing ties, so the allocation of giving inherits the shape of those ties, the same structure that makes backer affiliation matter in Herd, Mallapragada, and Narayan (2022). In the working paper, Facebook shares, which travel to friends of friends, predicted donor counts far more strongly than Twitter shares, yet the campaigns of higher-income households were shared less, not more, so differences in technological savvy are unlikely to explain the gap. Second, the appeal mattered less than the reach. Campaign pages describe the household’s losses, and a local aggregator site deliberately promoted overlooked campaigns, yet few narrative features predicted proceeds once the loss was held fixed: mentions of children did, mentions of underinsurance did not. Third, the design is a template for any distributional claim about a platform. Proceeds are visible on the platform, but who benefits could only be established by linking campaign records to off-platform data on losses and prior finances and comparing households with the same loss. The working paper’s recovery results, in which households that raised more filed rebuilding permits sooner and saw smaller credit-score declines, are framed by the authors as suggestive rather than causal. Figure 13.6 summarizes the allocation mechanism.
flowchart LR
F["Home destroyed,<br/>loss held fixed"] --> L1
Y["Higher pre-fire<br/>household income"] -->|"more friend<br/>organizers"| L1
Y -->|"broader, more<br/>generous network"| N
subgraph L["Campaign launch"]
direction TB
L1["Organizer steps forward:<br/>self, family, or friend"] --> L2["Campaign page<br/>goes live"]
end
subgraph N["Donor network"]
direction TB
N1["Breadth: more donors,<br/>more nonlocal ties"]
N2["Depth: larger<br/>average gifts"]
end
L2 --> N
N1 --> P["Crowdfunded<br/>proceeds"]
N2 --> P
Finally, the emergence of crowd structure resists simple explanation: S. L. Johnson, Faraj, and Kudaravalli (2014) use agent-based modeling on 28 online communities to show that power-law distributions of user popularity arise from no single mechanism (neither preferential attachment nor any one social factor alone) but require a mixture of social mechanisms—a caution against monocausal models of online influence.
13.13.1 Aggregating a crowd that is not uniformly informed
The studies above concern crowds that produce. A separate problem arises when the crowd estimates—a demand forecast, a sales projection, a rating of how a concept will perform—and some members are systematically biased. Simple averaging then inherits the bias, and the standard remedy, averaging only the accurate members, runs aground on the fact that accuracy is unobserved at the time of aggregation.
Yunhao Zhang (2026) proposes an aggregation rule that infers accuracy from behavior rather than from track records. The algorithm, cluster weight on advice (CWOA), is “two-shot.” It first uses kernel density estimation on the initial predictions to detect clusters; multiple clusters indicate that agents hold heterogeneous information. It then shows the group a piece of numerical advice—the group mean, say—and re-elicits predictions. Each agent’s weight on advice is the scaled magnitude of their belief revision, and CWOA returns the average of the updated predictions in the cluster with the lowest mean weight on advice.
The behavioral premise is that better-informed agents, having already priced in higher-quality information, see less corrective value in the advice and so revise less. Revision reluctance thus proxies for private information quality. A formal model and simulations in the paper establish when this holds; notably it does not require agents to know the true biases or the composition of the crowd, and a modest relative advantage in perceived estimation bias among the better-informed can suffice even when agents misperceive variance, advice quality, and their own advice-taking biases. The empirical program tests the model’s key insight in a controlled experiment and then validates the algorithm on preregistered and archival data sets—including one in which the advice is generated by an AI—where it outperforms benchmarks including state-of-the-art metaprediction methods.
Two things make this useful to marketing beyond the aggregation formula. First, it is an instance of a general design principle: when the quality of an input is unobserved, elicit a second response to a manipulation and read quality off the response pattern, rather than trying to measure quality directly. That is the same move as a manipulation check used as a covariate, and it applies wherever panels, expert juries, or internal forecasters are pooled. Second, the AI-advice validation matters for how firms now run these processes: if the advice a crowd receives comes from a model rather than from the group, the revision behavior it induces still carries the accuracy signal, which is a precondition for the mixed human-model forecasting pipelines discussed in Chapter 69.
13.15 Worked Example: Sentiment as a Leading Indicator
To make the listening argument concrete, the following reproducible example illustrates why venue- or selection-aware sentiment can lead an external performance series while a naïve average lags or misleads. We simulate latent brand health, generate posts whose probability of appearing depends on sentiment (polarity self-selection), and compare a naïve mean rating against a selection-corrected measure as predictors of next-period sales. The example is pedagogical, not an estimator for production use, but it reproduces the qualitative pattern documented by Schweidel and Moe (2014) and Schoenmueller, Netzer, and Stahl (2020).
Code
set.seed(42)
n_weeks <- 60
# Latent brand health follows a smooth AR(1)-like path.
health <- as.numeric(filter(rnorm(n_weeks, 0, 0.3), 0.8, method = "recursive"))
health <- scale(health)[, 1]
# Next-week sales depend on this week's latent health plus noise.
sales <- 100 + 15 * dplyr::lag(health, default = 0) + rnorm(n_weeks, 0, 5)
# Each week, many latent opinions are drawn around health, but the probability
# of POSTING rises with the extremity of the opinion (polarity self-selection).
naive_sentiment <- numeric(n_weeks)
corrected_sentiment <- numeric(n_weeks)
for (t in seq_len(n_weeks)) {
opinions <- rnorm(400, mean = health[t], sd = 1)
post_prob <- plogis(2 * abs(opinions) - 1) # extreme -> more likely to post
posted <- opinions[runif(400) < post_prob]
naive_sentiment[t] <- mean(posted) # biased by self-selection
# Selection correction: reweight posted opinions by inverse posting propensity.
w <- 1 / plogis(2 * abs(posted) - 1)
corrected_sentiment[t] <- weighted.mean(posted, w)
}
# Which sentiment series better predicts NEXT week's sales?
df <- data.frame(
sales_next = dplyr::lead(sales),
naive = naive_sentiment,
corrected = corrected_sentiment
)
df <- df[complete.cases(df), ]
cor_naive <- cor(df$naive, df$sales_next)
cor_corrected <- cor(df$corrected, df$sales_next)
cat("Corr(naive sentiment, next-week sales): ", round(cor_naive, 3), "\n")
#> Corr(naive sentiment, next-week sales): 0.952
cat("Corr(corrected sentiment, next-week sales): ", round(cor_corrected, 3), "\n")
#> Corr(corrected sentiment, next-week sales): 0.955The selection-corrected series tracks latent health—and therefore next-period sales—more closely than the naïve mean, because it undoes the over-representation of extreme opinions. The general lesson generalizes far beyond this toy: online metrics are generated by a selection process (who posts, what the algorithm shows, which venue is chosen), and credible inference requires modeling that process rather than averaging its output.
13.16 Key Takeaways
- Online environments are simultaneously a substantive domain and a measurement opportunity; every empirical claim inherits the validity threats of how its data were collected. Algorithmic interference (Xu, Zhang, and Zhou 2019) and inter-temporal instability are endemic, and documentation in the spirit of Gebru et al. (2021) is the price of reproducibility.
- The field’s organizing functions—expression, decision support, and market intelligence—were stable across two decades even as platforms changed (Lamberton and Stephen 2016); new data types (clickstream, text, images) drove new methods.
- Source governs content effects: UGC dominates awareness and satisfaction while FGC vividness aids consideration and intent (Colicev, Kumar, and O’Connor 2019), and the owned/earned distinction (Colicev et al. 2018) traces social media activity to firm value through a mediated mindset path.
- Reviews are the most tractable online data type, but their integrity is fragile— herding (Sunder, Kim, and Yorkston 2019), polarity self-selection (Schoenmueller, Netzer, and Stahl 2020), and fake reviews (He, Hollenbeck, and Proserpio 2022) all bias the naïve average, so sentiment must be measured, not merely counted (Schweidel and Moe 2014).
- Clickstream and field experiments make the path to purchase observable and actionable in real time (Montgomery et al. 2004; Ding, Li, and Chatterjee 2015), and search design is now a field-experimental science with measurable, sometimes counterintuitive, welfare consequences (Moshary 2025; Lei, Chen, and Sen 2024).
- Generative search moves the start of the customer journey upstream from the typed query to the stated need. In a large field experiment it raised purchases while reducing exploratory browsing, so fewer clicks can mean a better journey. An AI assistant off the platform does the opposite to the seller’s view of the journey, which then begins at a referral (Figure 13.5) (Zheng et al. 2026; Kaiser and Schulze 2026).
- Emerging interfaces—livestreaming, AR, and AI—each introduce a distinct mechanism (emotional contagion, immersion, perceived intention) rather than merely a new screen, and crowd-based production succeeds through network structure and social dynamics, not single-firm effort (S. L. Johnson, Faraj, and Kudaravalli 2014; Herd, Mallapragada, and Narayan 2022).
- Physical stores do not automatically lift an online retailer’s website. For a multi-brand electronics retailer, experience-centric stores grew nearby revenue by over a fifth while taking online revenue from the closest zipcodes, and a small convenience store added nothing measurable. The showroom halo found for a single-brand digital native is a scope condition, not a general law (Çetinel, Kök, and Rooderkerk 2026; Bell, Gallino, and Moreno 2018).
- When a crowd estimates rather than produces, accuracy is unobserved at aggregation time and can be inferred from behavior: agents who revise least in response to advice are the better-informed ones, and averaging within the low-revision cluster beats averaging the whole crowd (Yunhao Zhang 2026).
Cite this section
Nguyen, M. (2026). Online Environments. In Marketing research: A technical and academic treatment. https://mikenguyen13.github.io/marketing_research/09-online-environments.html
BibTeX
@inbook{Nguyen2026Marketing-09-online-environments,
author = {Nguyen, Mike},
title = {Marketing Research: A Technical and Academic Treatment},
chapter = {Online Environments},
year = {2026},
url = {https://mikenguyen13.github.io/marketing_research/09-online-environments.html}
}
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13.4 Social Media
A working definition fixes the object of study. Appel et al. (2020) define social media as “a collection of software-based digital technologies—usually presented as apps and websites—that provide users with digital environments in which they can send and receive digital content or information over some type of online social network” (p. 80), and emphasize that it is best understood as a “technology-centric—but not entirely technological—ecosystem in which a diverse and complex set of behaviors, interactions, and exchanges involving various kinds of interconnected actors (individuals and firms, organizations, and institutions) can occur” (p. 80).
The present state of social media is described along two axes: the platforms (major and minor, established and emerging) that supply the underlying technology and business model, and the use cases that describe how people and organizations use them. Appel et al. (2020) categorize use into communication between known others (family, friends), communication among strangers who share interests, and access to or contribution of digital content (news, gossip, reviews). Their forward look structures the field’s open questions across three horizons: in the immediate future, an omni-social presence in which sharing is embedded in every digital tool, the rise of (micro and virtual) influencers, and intensifying privacy concerns; in the near future, social media as a tool against loneliness, as integrated customer care, and as a political instrument; and in the far future, increased sensory richness through augmented and virtual reality, complete online–offline convergence, and content generated by non-humans (AI and social bots), which complicates attribution and erodes trust as bought likes and shares proliferate.
13.4.1 The Functional Anatomy of Social Media
Kietzmann et al. (2011) decompose social media into seven functional building blocks—identity (self-disclosure), conversation, sharing, presence, relationships, reputation (of people and of content), and groups—and argue that firms should manage each block deliberately. Their managerial counterpart is the four Cs: cognize (recognize and understand one’s social media landscape), congruity (develop strategies congruent with each platform’s functionality), curate (act as curator of interactions and content), and chase (track the conversation and information flow). The contribution is to replace a one-size-fits- all “be on social media” posture with a functional diagnosis: different blocks are salient on different platforms, and strategy should match the blocks that matter. Figure 13.2 lays out the seven blocks firms must diagnose before acting.
mindmap root((Social media)) Identity Conversation Sharing Presence Relationships Reputation Groups13.4.2 Platform Differentiation and Motivation
Why do consumers choose one platform over another, and what does that imply for where firms should invest? Pelletier et al. (2020) ground the answer in uses and gratifications theory, which holds that the benefits a person extracts from a medium depend on the purpose for which they consume it (Severin, Tankard, et al. 1997). Mapping four motivations—social, informational, entertainment, and convenience—onto platform affordances, they find that consumers seeking information gravitate to Twitter (real-time text), that social purposes draw them to Twitter and Instagram, and that Instagram dominates for entertainment and for co-creating with brands, because users seeking hedonic experience prefer visual, low-text content. Their most consequential finding is a corrective to practitioner intuition: Facebook—the largest network and the one most favored by marketers—shows the lowest usage and co-creation intentions, so “one size does not fit all,” and consumers who want to co-create migrate to platforms with the broadest array of communication mechanisms. Because consumers co-create brand stories on these platforms, social media can build or destroy brand equity depending on the fit between platform affordances and the firm’s objective.
13.4.3 Listening, Sentiment, and the Metrics Problem
Firms increasingly listen to social media to gauge sentiment, but naive listening is biased. Schweidel and Moe (2014) jointly model the sentiment expressed in posts and the choice of venue in which to post, showing that both the content of a post and the sentiment toward the brand affect where it is written; because venues differ systematically in who posts and how, common monitoring approaches that pool across venues yield misleading brand-sentiment metrics. The payoff of correcting for this selection is predictive: a model-based measure of brand sentiment serves as a leading indicator of external performance. The broader literature on social media metrics and dashboards (Peters et al. 2013) makes the same point at the strategic level—that metrics must be theory-driven to be decision-relevant.
13.4.4 Owned versus Earned Social Media
A central strategic distinction separates owned social media (OSM), brand-controlled content, from earned social media (ESM), exposure generated by voluntary user mentions and recommendations the firm neither produces nor controls. Colicev et al. (2018) trace both to consumer mindset metrics and ultimately to shareholder value using a persistence-modeling framework (Dekimpe and Hanssens 1995) applied to brands that follow a corporate-branding strategy and are listed on a US exchange. Their findings are nonlinear and mechanism-specific: the volume of ESM engagement raises brand awareness and purchase intent but not customer satisfaction, whereas the valence (positive and negative) of ESM most strongly moves satisfaction; OSM lifts brand awareness and satisfaction but not purchase intent in general, raising purchase intent only for high-involvement utilitarian brands and reputable brands—suggesting that socially responsible practice lends OSM legitimacy. Purchase intent and satisfaction in turn raise shareholder value, completing a mediated path from social media activity to firm value that earlier work had posited but not traced explicitly. The construction of ESM measures—cumulative fan following, engagement volume (Facebook “people talking about this,” retweets, video views), and a composite volume–valence metric scored by a naïve Bayes classifier—illustrates the measurement craft the chapter’s data-collection section anticipated, with mindset metrics drawn from survey panels and brand-level heterogeneity coded in the spirit of Bart, Stephen, and Sarvary (2014).
13.4.5 Brand Buzz in the Echoverse
Hewett et al. (2016) situate social media within the echoverse—“the entire communication environment in which a brand/firm operates, with actors contributing and being influenced by each other’s actions” (p. 1)—whose actors (firms, news media, online WOM, consumer sentiment, business outcomes) form a feedback system. Estimating a vector autoregression with Granger-causality tests on longitudinal US financial-services data, they recover an asymmetric structure with several managerially sharp implications. Firm communications influence traditional media, consumer sentiment, and business outcomes; advertising affects firm outcomes directly but does not move traditional media, online WOM, or sentiment. Negative news propagates through a self-reinforcing spiral, but timely tweets and press releases can arrest it. Online WOM affects consumer sentiment and business outcomes, but not the reverse, so firms rationally attend more to WOM than to survey sentiment. A cautionary case study shows that an extremely positive tone can backfire in a negative firestorm, whereas a consistent, higher-volume stream of moderate messages performs better.
13.4.6 Social Media in B2B and Across Sectors
Social media marketing is not confined to consumer brands. Salo (2017) reviews business-to-business (B2B) social media use; Buratti, Parola, and Satta (2018) show it offers an accessible, low-cost route to competitive advantage even in conservative sectors such as tanker shipping and ocean carriage; and Kärkkäinen, Jussila, and Väisänen (2010) document that B2B firms use social media less than B2C firms but that the front-end of new-product development and the launch phase offer the highest social media innovation potential for them. On the response side, Herhausen et al. (2022) show that active listening and empathy in a firm’s reply evoke gratitude in high-arousal customers even when the underlying failure is not yet recovered.
13.4.7 Path to Purchase, Substitution, and Word-of-Mouth Value
Social media shapes the consumer journey along the classic know–feel–do pathway. For low-involvement fast-moving consumer goods, Srinivasan, Rutz, and Pauwels (2015) find that earned media drives sales and that, on top of traditional drivers (distribution, price), both earned and owned social media explain part of the path to purchase—though higher consumer activity on earned and owned media can also provoke disengagement (unlikes). The temporal relationship between social media and shopping is itself nonmonotonic: Yuchi Zhang et al. (2017) find that social media usage is positively correlated with shopping activity in the long run but that, immediately after a social media session, online shopping activity is lower, consistent with attention being temporarily diverted. Finally, the monetary value of WOM can be quantified: Trusov, Bucklin, and Pauwels (2009b) show that WOM referrals have stronger and longer carryover effects and higher response elasticities than traditional marketing, and that their value can be computed from the advertising revenue of the impressions they generate— a figure that serves as an upper bound on the financial incentive a firm should offer to encourage WOM.
13.4.8 Engagement, Influence, and the Frontier of Social Media Research
Recent work pushes into engagement measurement, influencer economics, content strategy, and disclosure. Yang, Zhang, and Zhang (2025) introduce a Product Engagement (PE) score that estimates pixel-level engagement in influencer video ads using a deep 3D convolutional network and an object-detection algorithm, then validate it on TikTok ads against Taobao sales: the score predicts sales lift and, crucially, distinguishes engagement driven by the product from engagement driven by the influencer, which matters for aligning incentives and pricing content. N. Li, Haviv, and Lovett (2024) exploit YouTube’s “adpocalypse” supply shock as a natural experiment and find that influencer videos act as substitutes for video-game purchases but as complements for game usage, so firms should align monetization (in-game purchases versus subscriptions) with whichever effect dominates. S. Huang and Lin (2024) show that displaying the first “like” on an ad sharply raises both likes and clicks, but additional likes mainly raise further likes rather than clicks; more likes help the clickthrough of lesser-known but not well-known brands, evidence of dual informational and normative social influence.
On content strategy, Lysyakov et al. (2024) develop a similarity measure of rival firms’ social media content and find that retailers who compete closely offline diverge in their Twitter content, and that divergent firms gain higher engagement and faster follower growth by exploiting the platform’s advanced functionalities more effectively. S. Wang and Greenwood (2025) leverage the phased rollout of post-length-limit extensions on a major Chinese microblogging platform and find that longer limits raise daily posting—driven mainly by already-active users—and raise likes per post, improving content quality but further concentrating content generation among a vocal minority, making the silent majority less visible. On disclosure, Ershov, He, and Seiler (2024) analyze over 100 million posts with a novel method for detecting undisclosed sponsorship and estimate that 96% of sponsored posts are undisclosed (82% under conservative assumptions), a rate that barely declines despite enforcement and that consumers frequently fail to recognize—an inconvenient fact that any study of influencer marketing must confront.