Shuichiro Ogawa
日本語

Notes · updated 2026-08-30

One Person Saying It Three Times, Three People Saying It Once Each

Hear the same opinion three times. Does it land differently on the listener depending on whether one person said it three times, or three people each said it once?

What Weaver, Garcia, Schwarz, and Miller reported in 2007 is that it barely does. Across six experiments, participants who heard a single person repeat an opinion estimated that the opinion was widely supported within the group. The strength of that estimate was nearly identical to what participants produced after hearing the same opinion from multiple people.

The trouble starts here: the effect did not disappear even in the condition where participants were explicitly told the speaker was a single person. Knowing that the source was singular, and being able to bring that knowledge to bear on the estimate, turn out to be different things.

The paper’s subtitle is “A repetitive voice can sound like a chorus.”

Worth confirming first is that this result predates generative AI by nearly two decades: it is from 2007. The fragility of reading “I see it a lot” as “it happens a lot” was already confirmed in the laboratory fifteen years before generative models arrived.

So what did generative AI change? Or did it change nothing at all? This note gathers 303 academic sources bearing on that question, and sorts out what has already been measured from what has not. The classic material, gathered up through around 2024, was organized into five lines of inquiry; the last three years, from 2023 to 2026, were then added across five further lanes; and finally, the differential check against echo chamber research, the closest neighboring concept, was verified across two further lanes.

Reading Population Size from Frequency

Why, in the first place, do people infer headcount from how often they see something?

The availability heuristic that Tversky and Kahneman (1973) formalized is described as a strategy that repurposes the ease of recalling instances for judging frequency and probability. The strategy has a rational basis: things that are genuinely frequent are also easier to recall. The problem is that ease of recall is also shaped by factors other than frequency, such as prominence, media coverage, and recency, and that is where the systematic bias creeps in.

Zajonc’s (1968) mere-exposure effect is the affective version of the same strategy. Repeated exposure alone raises liking for a target, requiring no reward, no argument, and no conscious memory of the exposure.

The social sampling model of Galesic, Olsson, and Rieskamp (2012, 2018) more directly addresses how people estimate a population’s distribution. The model treats people as extrapolating from the limited sample of their own social relationships to the population as a whole. Its core claim is that much of what looks like bias (self-enhancement, self-deprecation) can be derived from the sampling process itself rather than from a cognitive defect.

Once sampling is skewed, estimation is skewed. Ross, Greene, and House’s (1977) false-consensus effect, shown across four studies, is the tendency to overestimate how common one’s own choices actually are. Mullen et al.’s (1985) meta-analysis pooled 115 hypothesis tests and confirmed the effect holds up reliably at around r≈.31. The reverse phenomenon exists too: Suls and Wan (1987) reported false uniqueness, the tendency to underestimate how common one’s own state is.

At the group level, this misestimation drives behavior. Perkins and Berkowitz (1986) surveyed 1,116 students and measured a gap in which individuals’ own attitudes were moderate, yet they misjudged those around them as more permissive than themselves. Prentice and Miller (1993), in a longitudinal study at Princeton, showed that students adjusted their actual drinking to match this mistaken perception of the norm. Cialdini, Reno, and Kallgren’s (1990) three field experiments, using litter scattered in a parking lot, confirmed that descriptive norms, beliefs about what others actually do, shape behavior.

Bicchieri (2006, 2017) builds this structure directly into the definition of a norm itself. In her framework, a social norm requires both an empirical expectation (a belief about what others actually do) and a normative expectation (a belief about what others think should be done). The empirical expectation is built from observed frequency. In other words, “seeing it a lot” is a component built directly into the definition of a norm.

The Population on Screen Does Not Match the Census

The premise that frequency mirrors population has long been questioned in mass-media research.

Gerbner et al.’s (1980) cultivation theory argued that heavy television viewers internalize the frequency distribution of the television world as reality. Testing this claim takes the form of cross-referencing content analysis against audience surveys.

On the content-analysis side, a body of research has accumulated directly comparing on-screen frequency against statistical rates. Dixon and Linz (2000) analyzed local news in Los Angeles and Orange Counties and quantified that Black and Latino individuals were overrepresented as lawbreakers relative to actual crime statistics, while white individuals were overrepresented as protectors of the law. Jacobs, Claes, and Hooghe (2015) measured the occupational world of Belgian primetime programming against occupational prestige scores and showed its divergence from the actual labor market. Baruah et al. (2022) ran computational text analysis on subtitles from over 136,000 IMDb titles and tracked the trend in occupational mentions across seven decades.

Cultivation theory itself, however, has drawn strong criticism. Potter (1993, 2014) raised doubts about the interpretability of its effects, pointing to coarse exposure measures, an assumed linearity, and arbitrariness in cultivation indicators. Hermann, Morgan, and Shanahan’s (2021) three-level meta-analysis pooled 406 samples and 3,842 effect sizes and reported r=.107; even granting that an effect exists, it is not a large one.

Worth noting here is what these studies actually theorized. What was measured was the size of the gap and the gap’s effect on viewer cognition. The question of why frequency can serve as a cue for prevalence in the first place, and under what conditions that strategy breaks down, was not itself the subject.

The Structure Where a Few Write the Bulk Predates AI

Generative AI has certainly made it possible for one person to produce a large volume alone, but the phenomenon of output volume decoupling from the number of authors has already been observed in human-only environments.

Pew Research Center (2019), using a probability-sample panel (Ipsos KnowledgePanel, n=2,791), measured that the top 10% of U.S. adult Twitter users produced 80% of all tweets. Restricted to politics, the skew was even sharper: 6% of all users wrote 73% of national-politics tweets. Van Mierlo (2014), from behavioral logs on four health social networks, reported that 1.3% of users generated 74.7% of posts.

Barberá and Rivero (2015) analyzed roughly 70 million election-period tweets from Spain and the United States and showed that political posters skewed male, urban, and ideologically extreme. Bail et al. (2018) similarly suggest that on Twitter, political speech is dominated by a small number of extreme voices that are overexposed and do not function as a proxy for the opinion distribution of the general population.

How is one person able to send so much? Rao and Reiley (2012) formalized this as the economics of spam, working from the cost structure. When the marginal cost of sending is close to zero, send volume becomes independent of both the number of senders and the number of recipients. They estimated the ratio of the sender’s internal benefit to the social cost at roughly 1 to 100.

Once deliberate operation enters the picture, the scale grows further. King, Pan, and Roberts (2017), working from a leaked cache of roughly 44,000 posts by the Chinese government, derived an estimated annual scale of 450 million posts and showed that the purpose was strategic distraction rather than argumentative engagement. Linvill and Warren (2020) classified roughly 3 million tweets from Russia’s IRA into five types and revealed a division-of-labor structure. Bradshaw and Howard (2019) surveyed the budgets, staffing, and organizational structures of cyber troops across 70 countries.

The same outcome can be derived from the structure of the observer’s side as well. Lerman, Yan, and Wu’s (2016) majority illusion formalizes how a correlation between a network’s degree distribution and an attribute alone can make a globally rare state look like a majority under an individual’s local observation. No one here is lying, and no headcount is being faked. Even so, local frequency departs from the global ratio. Alipourfard et al. (2020) extended this to directed networks and treated it within a unified framework alongside the friendship paradox.

Stella, Ferrara, and De Domenico (2018) showed, using data from the Catalan independence referendum, that bots can actively manufacture this illusion by selectively targeting influential human users from the network’s periphery.

Detecting Fabrication Has Always Meant Finding Fake Personas

Fabricating a majority through mass output has a lineage of countermeasures. What that lineage has relied on as evidence is worth examining closely.

Ratkiewicz et al.’s (2011) Truthy detected memes spreading from centralized clusters of accounts using topological and content features. Kumar et al. (2017) identified 3,656 sockpuppets across nine discussion communities, relying on linguistic and behavioral similarity between multiple accounts operated by the same individual. Cresci et al. (2017) encoded behavioral sequences as “digital DNA” and found spambot clusters through matching signatures across accounts. Giglietto et al.’s (2020) CooRnet detects coordinated behavior in which multiple pages repeatedly share the same URL within a short time window.

What these share is that they use relationships among multiple fake personas as evidence. The unit of detection is the account, and manipulation presupposes that the account is performing as a human.

The definitions themselves share the same structure. Kovic and Rauchfleisch (2018) defined digital astroturfing as “top-down deceptive manipulation that mimics spontaneous activity by autonomous citizens.” Woolley and Howard’s (2017) definition of computational propaganda includes as a requirement “the deliberate distribution of misleading information.” The corporate astroturf organizations Cho et al. (2011) address also carry explicit strategic intent. Luca and Zervas’s (2016) review fraud is likewise explained by an economic motive: reputation manipulation.

Starbird, Arif, and Wilson (2019) moved past the bot-versus-troll dichotomy to reconceive information operations as collaborative work with a human crowd, but even there, how to distinguish organized manipulation from organic crowd behavior remains an unresolved problem.

In short, existing frameworks make two things the condition for something to count as manipulation: deceptive intent, and the act of impersonating a persona.

How Far Has the Volume of Generated Content Been Measured

For the period after generative AI, empirical measurement of volume is accumulating.

Kobak et al. (2025, Science Advances) tracked over 15 million PubMed abstracts from 2010 through 2024 and, through excess-vocabulary analysis, detected a surge in certain words (such as “delve” and “underscore”) after ChatGPT’s public release. From this they estimate that at least 10% of 2024 abstracts, and up to 30% in some fields, had gone through LLM processing. It is an estimate that applies the excess-mortality analytical method to vocabulary.

La Cava, Aiello, and Tagarelli (2025) surveyed 51 subreddits from 2022 through 2024 and measured machine-generated text reaching as high as 9% monthly in some communities. Brooks, Eggert, and Peskoff (2024), using two detectors, detected an increase in AI-generated content among Wikipedia articles created after GPT-3.5’s release (a lower-bound estimate given the nature of the detectors used). Thompson et al. (2024) showed, from patterns in parallel multilingual translation, that a substantial share of web content in low-resource languages derives from low-quality machine translation.

There is also measurement of the reader’s own ability to discriminate. Jakesch, Hancock, and Naaman (2023), across 6 experiments with over 4,600 participants, showed that people cannot reliably distinguish AI-generated self-introductions from human-written ones. What participants relied on were cues, such as first-person pronoun use, contractions, and mentions of family, that in fact were not useful for discrimination.

How Generated Distributions Diverge from Population Distributions

Apart from volume, the distribution within generated content’s substance has been measured as well.

Luccioni et al. (2023) generated and analyzed over 96,000 images from DALL-E 2 and Stable Diffusion and quantified overrepresentation of whiteness and maleness, and underrepresentation of marginalized identities, relative to U.S. labor statistics. Bianchi et al. (2023) showed that Stable Diffusion’s output amplifies racial and gender stereotypes, and that this bias is not corrected by user-side counter-prompting or guardrails.

Language models’ opinion distributions have been measured similarly. Santurkar et al. (2023) built OpinionQA and quantified that the gap between a language model’s opinion distribution and the opinion distributions of 60 U.S. demographic groups is as large as the partisan divide between Democrats and Republicans over climate change. Conditioning on demographics did not correct this gap.

This point had already been problematized from the methodology side. Argyle et al. (2023) argued that GPT-3 conditioned on demographics can mimic the response distributions of human subgroups, and proposed the concept of the silicon sample. Bisbee et al. (2024) pushed back with disconfirming evidence, showing that ChatGPT-3.5 given personas based on ANES demographics exaggerated the extremity and confidence of responses relative to the actual partisan divide, and that the distribution grew unstable under small prompt changes and over time. What is being contested here is whether AI output can be treated as a proxy for a population, and the object under scrutiny is researchers’ own inference.

There is also measurement of the collective outcome. In Doshi and Hauser’s (2024) randomized experiment, stories from writers assisted by an LLM were individually rated highly, yet as a group they grew similar to one another, and collective diversity fell. Anderson, Shah, and Kreminski (2024), in a comparative user study with 36 participants, confirmed that ChatGPT users generated ideas that were more semantically similar to one another than those of users of alternative tools.

At the level of the information environment as a whole, Peterson (2025) used the concept of knowledge collapse to argue, through theory and simulation, that as AI lowers the cost of accessing information, societal attention skews toward central knowledge and peripheral knowledge is lost. Wright et al. (2025) measured epistemic diversity across 27 models, 155 topics, and 12 countries and demonstrated that every model showed lower diversity than a basic web search.

On the loop by which a model learns from its own output, Shumailov et al. (2024, Nature) showed that recursive training causes the tails of a distribution to be systematically lost. Alemohammad et al. (2024) likewise reported that a self-consuming loop produces collapse within a few generations. However, Gerstgrasser et al. (2024) offer disconfirming evidence that in settings where synthetic data accumulates rather than replacing existing data, collapse can be avoided; the point remains unsettled.

What these loops address is the training data of the next-generation model. What happens when humans, as readers, are exposed to the same distribution is a separate question.

Over These Three Years, How Far Has Volume Been Measured

What precedes is the picture that had solidified by around 2024. Between 2023 and 2026, measurement in several domains has advanced to where the order of magnitude is visible.

The academic side has been measured in the finest detail. Liang et al., at ICML 2024, estimated that 6.5% to 16.9% of the body text of peer reviews at ICLR 2024, NeurIPS 2023, CoRL 2023, and EMNLP 2023 had been substantially altered by an LLM. The rate ran higher among low-confidence reviews, reviews submitted close to the deadline, and reviews that did not respond to a rebuttal. Rao et al. (2025), using a statistical watermark-embedding method, reported detecting over 10,000 ICLR 2021 submissions and over 28,000 ICLR 2024 submissions with zero false positives. Liu et al. (2025), from over 2 million full texts on PubMed Central, estimate that adoption of AI-assisted writing grew 400% among non-English-speaking researchers and 183% among English-speaking researchers. The growth was larger among researchers with lower citation counts and lower-ranked affiliations.

The point of entry to information has also begun to be measured. Allaham and Diakopoulos (2026) audited 712 queries’ worth of cited sources across ChatGPT, Copilot, Gemini, and Perplexity, and estimated that about 16% of cited sources were already AI-generated content. Grossman et al. (2026), across 11,500 real queries, measured that the overlap between Google Search’s cited sources and generative search engines’ cited sources stayed below a Jaccard coefficient of 0.2. In Huang et al.’s (2026) audit, hedging language fell 60% in generative-search responses, and Wikipedia was overrepresented while social media was underrepresented among cited sources.

On the ratio for the web as a whole, estimates diverge widely. Spennemann (2025), from the frequency of characteristic words, estimates that 30% to 40% of active pages have AI-generated origins, though the method is a simple one that uses no detector. Estimates from detection vendors sometimes produce even larger figures. These, however, rely on the vendor’s own product detector, and threshold validity has not been independently verified. These are treated as the source’s own claims and are not cited here as fact.

On the cost side, Musser (2023) modeled the cost of generating content for an influence campaign and estimated that even at a low practical LLM reliability of around 25%, it comes in cheaper than an all-human operation, and that at higher reliability the saving can reach up to 70%. The cost of the watermark-removal attack Cheng et al. (2025) demonstrated is $0.88 per million tokens.

The scale of generation without intent has also been measured. Horne and Gruppi (2024) built a dataset collecting over 7.9 million articles across two and a half years from 1,093 pink-slime sites posing as local news. Their motive is not opinion manipulation but advertising revenue and search ranking. Schmitz et al. (2026) documented 84 cases across 11 jurisdictions in which AI agents flooded government services with applications. No malicious actor and no deception is present here. Agents that acted for citizens’ benefit ended up causing a surge in demand.

Where the Detecting Side Has Stalled

If volume can be measured, can discrimination not follow? The results from these three years say that optimism is not warranted.

The detectors themselves carry bias. Liang et al. (2023) showed, across seven commercial detectors, that a majority of essays written by non-native speakers were misclassified as AI-generated. Al Ali et al. (2026), however, could not reproduce the same bias in Czech, and suggest the bias may depend on language and period.

Watermarks are vulnerable to attack. Cheng et al.’s (2025) self-information-based paraphrase attack achieved a near-100% removal success rate against seven state-of-the-art schemes. Wu et al. (2026) showed that merely averaging the output distributions of three to five models pushes detection scores below threshold, while at the same time improving output quality by 27.5%. An et al. (2026) went further, using knowledge distillation to replicate a watermark signal and forging unrelated generated content to look like a specific model’s output.

Provenance standards have not passed independent evaluation either. Golaszewski et al. (2026) analyzed the C2PA specification with formal methods and concluded that the current specification does not achieve the security goals it claims, and is not yet usable for high-trust applications such as journalism, financial disclosure, or legal evidence.

Bot detection loses performance in the face of LLMs. Feng et al. (2024) showed that LLM-based evasion strategies cut existing detectors’ performance by up to 29.6%. Dawkins et al. (2025) confirmed, across a dataset of over 500,000 items, that detectability drops sharply under the realistic setting where an attacker keeps a fine-tuned model private. Puccetti et al. (2024) showed that simply fine-tuning Llama on 40,000 Italian news articles was enough to produce articles humans find hard to discriminate.

Experiments Where Artificial Popularity Became Real Popularity

That a distribution initially false can later become real has already been confirmed experimentally, prior to generative AI.

Salganik, Dodds, and Watts (2006, Science) built an artificial music market with 14,341 participants and compared, across eight parallel worlds, conditions where other people’s download counts were visible against conditions where they were not. When social signals were visible, both the inequality and the unpredictability of success increased. Song quality alone no longer determined what became a hit.

Salganik and Watts (2008), using the same framework, deliberately displayed inverted popularity rankings. Popularity that was initially false went on to produce real popularity later. The paper’s title is “Leading the herd astray,” and its subtitle names the self-fulfilling prophecy explicitly. Also important is that full self-fulfillment did not occur. The best songs recovered their popularity over the long run, and the false distribution did not become fixed for the market as a whole.

Muchnik, Aral, and Taylor (2013, Science) randomly assigned an upvote, a downvote, or no manipulation to the initial comments on over 100,000 posts on a news-aggregation site. The upvote manipulation significantly raised the final score, and its effect was asymmetric relative to the downvote condition.

What these experiments manipulated was an evaluative signal (a rank, a vote count) attached to content after the fact. Participants viewed that signal while recognizing it as “information about other people’s choices.”

There is also a separate experimental tradition dealing with the frequency of observed usage itself. Centola and Baronchelli (2015) observed a group of roughly 100 people establishing a convention with no top-down coordination. Centola et al. (2018, Science) identified a critical mass: once a minority coalition exceeds roughly 25% of the group, an existing norm flips rapidly, while below 25% the attempt fails.

On the theory side, Merton (1948) formalized the process by which a false definition of a situation calls forth behavior that makes an initially false belief come true, and Biggs (2009) argued the concept should be restricted to cases “where the actor is unaware that their own belief constituted the reality.” MacKenzie and Millo (2003) and MacKenzie (2006) show from historical records that the Black-Scholes option-pricing theory did not discover a pre-existing price pattern but instead became accurate after the fact, once practice conforming to the theory had spread. Marti and Gond (2019) organized this process into a staged model.

Hacking’s (1986, 1995) looping effect addresses a double circuit in which classification changes the classified, and the change in the classified rewrites the classification in turn. What drives this, however, is the discrete act of classification by an expert community, which is a different order of mechanism from the statistical skew of mass-produced output.

The theory of information cascades (Bikhchandani, Hirshleifer & Welch 1992; Banerjee 1992) showed the conditions under which it becomes individually optimal for someone observing predecessors’ actions to ignore their own private information and imitate. Anderson and Holt (1997) reproduced this in the laboratory. A cascade can start from trivial information, and it can collapse from trivial information too.

Kuran’s (1995) preference falsification and Willer, Kuwabara, and Macy’s (2009) false enforcement address the mechanism by which a norm that no one privately supports is nonetheless kept apparently in force.

Does Seeing Generated Content Move the Judgment of What Is Normal

What the experiments in the previous section manipulated was an artificial popularity signal. Experiments that use generative AI itself as the stimulus have appeared in these last three years.

Glickman and Sharot (2025, Nature Human Behaviour) traced, across three experiments, how repeated human-AI interaction amplifies judgment bias and how humans then learn from that amplified distribution in turn. Participants totaled 1,401. In the third experiment, participants were shown three Stable-Diffusion-generated images of a “financial manager,” 1.5 seconds each. Asked afterward who looked most like a financial manager, the share choosing a white man rose from 32.36% to 38.20% (p=0.04). The control group showed no significant difference.

AlDahoul, Rahwan, and Zaki (2025) obtained a result in the same direction using AI-generated face images. Exposure to images that included diversity reduced biased perceptions of race and gender; exposure to images that did not include it increased them. The effect occurred regardless of whether the images were disclosed as AI-generated.

Evidence has also emerged from a real platform on manipulation of algorithmic visibility. Brady et al. (2026, Nature, a preregistered report) randomly assigned 2,000 people on Bluesky to three feed types over eight weeks spanning the 2024 U.S. presidential election. The engagement-optimizing feed amplified divisive content and lowered the accuracy of social-norm perception. The algorithm that diversified extremity improved norm perception while preserving satisfaction.

Negative results stand alongside these, however. Geber and Stahel (2026), in an experimental survey comparing recommendation types (N=1,021), reported that the type of recommendation itself had no significant effect on perceived social norms. Liu et al. (2025, PNAS), across four experiments manipulating actual YouTube recommendations (roughly 9,000 participants total), showed that even artificially constructing filter-bubble conditions produced no detectable short-term polarization effect on policy attitudes.

Multiple pieces of evidence show that direct exposure to generated content’s substance moves judgment, while evidence also exists, at the same time, that manipulating visibility or recommendations alone does not move it, or does so only to a limited degree. Where the mechanism lies is not yet settled.

Perceived Frequency and the Actual Ratio

Research directly comparing perceived ratios against measured ratios has also grown over these three years.

Lee, Neumann, Zaki, and Hancock (2025, PNAS Nexus) had 1,090 U.S. adults estimate the share of users who post harmful content, the share who share fake news, and the share of extreme high-volume posters, and compared these against measured values. The estimates overstated the true figures by up to roughly 100-fold.

In Møller et al.’s (2026) social-media simulation experiment (a representative U.S. sample of 680), the treatment group’s actual rate of AI-assistance use reached as high as 100%, while their estimate of other people’s AI use stayed at 38% to 44%.

On climate change, Geiger et al. (2025, Psychological Science) confirmed, across 11 countries (n=3,653) and 55 countries (n=60,230), that the share of people in favor is consistently underestimated, by as much as 20.8 percentage points. An intervention presenting consensus information, however, moved behavioral intention hardly at all.

There are cases where correcting misperception does work. In Voelkel et al.’s (2024, Science) megastudy of n=32,059, an intervention correcting misperceptions of the opposing party’s views ranked among the most effective at reducing antidemocratic attitudes.

On the theory side, Asami and Kishishita (2025) and Gavrilets, Karl, and Gelfand (2026, PNAS) have formalized the conditions under which, the moment conformity mixes into expressed behavior, the inference that reads a population’s attitude from others’ observed frequency collapses into a self-reinforcing error. Neither builds AI or algorithms explicitly into the model.

Schroeder et al. (2026), in a Science policy forum, warned that AI-driven swarms of personas could create the illusion of a “synthetic consensus,” distorting public opinion and norms in a way detached from the actual scale of genuine support. This is a policy proposal, not research backed by empirical data.

When Experts Used Frequency as a Proxy for Population and Got It Wrong

The same failure occurs not only in lay intuition but in professional measurement.

Google Flu Trends, analyzed by Lazer, Kennedy, King, and Vespignani (2014, Science), attempted to estimate influenza incidence from search frequency. Over the winter of 2012 to 2013, this estimate came in at more than double the CDC-reported figure. The causes identified were a shift in search behavior, as anxious people who were not infected began searching too, and a change to the search service’s own algorithm.

What moved the frequency here was the search behavior of real, anxious human beings. Frequency and incidence diverged, but the frequency itself remained a record of actions actually taken by part of the population.

The same failure recurred repeatedly in election forecasting. Gayo-Avello’s (2013) meta-analysis concluded that the predictive power of Twitter-based election-forecasting research has been overstated. Metaxas, Mustafaraj, and Gayo-Avello (2011) showed that the accuracy of published methods did not exceed chance level. Cohen and Ruths (2013) demonstrated that the over-90% accuracy reported for political-stance estimation models was inflated by roughly 30 percentage points due to a biased method of collecting validation data.

Criticism of representativeness has been organized methodologically. Ruths and Pfeffer (2014, Science) argued that the bar should be raised for research using platform data, naming the contamination of “senders that are not human in the first place,” such as bots and organizational accounts, as a threat to validity. Tufekci (2014) organized the problems of reliance on a single platform, sampling bias from hashtags, and users’ visibility-avoidance behavior. Boyd and Crawford (2012) argued that big data is neither objective nor exhaustive, but merely reflects the platform that produced it and its users.

The vocabulary these critiques use is sample bias. In the total-survey-error framework systematized by Groves and Lyberg (2010), a mismatch between the frame population and the target population is called coverage error. Sen et al.’s (2021) TED-On extends this thinking to digital trace data, defining types such as platform coverage error and user self-selection error.

If bias is a sampling problem, it can be corrected statistically. Wang, Rothschild, Goel, and Gelman (2015) showed that even from an extremely non-representative sample, Xbox users, multilevel regression and poststratification could predict the 2012 U.S. presidential election with high accuracy. Diaz et al. (2016) formalize online data as “an imperfect continuous panel survey” and offer a correction framework.

The premise on which correction rests is that the sender is a real individual located somewhere within the population, and that only the weighting allocation is skewed.

Generated Content Reaches the Measuring Instruments Too

It is not only laypeople who misread frequency. The measurement apparatus itself has, over these three years, absorbed a different form of contamination.

Westwood (2025, PNAS) showed that an autonomous LLM agent given a demographic persona could evade a survey’s quality controls, including attention checks and reverse-shibboleth questions, in 99.8% of 6,000 trials. The paper states that the premise underlying survey research, that a consistent response is a human response, can no longer be sustained. NORC’s (2026) literature review organized existing industry estimates of the fraudulent-response rate in nonprobability surveys at 15% to 30%, reaching as high as 45% on some platforms. Asher et al. (2026), across three Prolific studies (N=928), measured keystrokes and built a method for detecting AI-assisted cheating from pasted text and abnormally sparse keystrokes.

Debate over using language models as a proxy for respondents has also advanced. Dominguez-Olmedo, Hardt, and Mendler-Dünner (2024) evaluated 43 models on the U.S. Census Bureau’s ACS and showed that bias toward response order and labels dominates, and that correcting for it pushes responses toward uniform randomness. Ma et al. (2026), using the U.S. Survey of Public Participation in the Arts, generated over 270,000 proxy responses and reported that the relational structure among preferences nearly vanishes in the silicon sample. Kim et al. (2025) compared a nationally representative U.S. survey (N=978) against six models and measured that the models compress opinion variance by an average of 27.9% and systematically misrepresent intersectional groups.

The conditions of observation itself have also changed. On X’s 2023 move to paid API access, Blakey (2024) laid out how it effectively ended academic access, and Murtfeldt et al. (2024), tracking 33,306 studies bibliometrically, showed that the growth rate of such research turned from +25% to −13% annually. Researcher data access under Article 40 of the EU Digital Services Act has begun to move, but Goanta et al. (2026) point to a structural impasse in which researchers must file specific requests without knowing the full extent of a platform’s internal data.

Where This Differs From Echo Chamber Research

Isn’t what has been said so far the same thing echo chamber research has already said? On the point that an observed opinion distribution departs from the actual distribution, the two do overlap. This section checks that overlap from the outside.

Where the Cause Has Been Located

Even within echo chamber research, where the source of the divergence lies is not agreed upon.

Sunstein (2001, 2017) locates it in the receiver’s own selective self-filtering. Pariser (2011) locates it in the algorithm’s implicit personalization. Cinelli et al. (2021, PNAS) compared over 100 million items across Gab, Facebook, Reddit, and Twitter, and identified network homophily as the primary cause. Del Vicario et al. (2016, PNAS) likewise treat selective exposure as the main driver of diffusion.

Bakshy, Messing, and Adamic (2015, Science) separated these two factors using 10.1 million Facebook users. Algorithmic ranking alone reduces cross-cutting content by about 15%. Subsequent individual clicking behavior reduces it by a further roughly 70%. Their conclusion is that the effect of individual choice is larger.

González-Bailón et al. (2023, Science), in an aggregation at the scale of 208 million people, separately measured three stages: the inventory of articles that could have appeared in the feed, what was actually seen after algorithmic selection, and what was engaged with.

What They Share: The Counted Unit Is Human

Though the locus differs, one premise is shared. Behind each observed item stands one human being who actually holds that opinion.

This follows from the structure of the methodology. Cinelli et al. (2021) treat their 100-million-plus items as utterances by real users; Barberá et al. (2015) estimate the ideological position of 3.8 million accounts; Bakshy et al. (2015) take a real population of 10.1 million users as the population of reference. The correspondence, that a node is a human being, is the starting point.

Among the 24 echo-chamber studies this note collected, none was found to state this premise explicitly. It would be more accurate to say there was no need to state it. Without a reason to doubt it, a premise goes unwritten.

The Weight of Disconfirming Evidence

On how strong echo chambers actually are, the accumulation of disconfirming evidence is substantial.

Flaxman, Goel, and Rao (2016, POQ), from the browsing histories of 50,000 U.S. users, showed a two-sided pattern in which browsing via search and social media both widened average ideological distance and increased cross-cutting exposure. Guess (2021, AJPS), from behavioral data, reported that the overlap in media diets between Democratic and Republican supporters was about 65% in 2015 and about 50% in 2016. Dubois and Blank (2018), in a representative UK sample (N=2,000), showed that people with high political interest and people with diverse media diets tend to avoid echo chambers. Möller et al. (2018), from a simulation over 21,973 Dutch newspaper articles, confirmed that several recommendation logics produce recommendations about as diverse as those of human editors.

Reviews point the same way. Zuiderveen Borgesius et al. (2016) concluded that the empirical evidence for concern about filter bubbles is thin, and Bruns (2019) criticized the discourse itself as a form of media panic. The Reuters Institute review by Arguedas et al. (2022) concludes that echo chambers are far more limited than conventional wisdom holds and that no evidence supports the filter-bubble hypothesis.

It has also been pointed out that the conclusion depends on how it is measured. Terren and Borge-Bravo (2021), across 55 reviews, reported a split in which studies using behavioral history support the existence of echo chambers while studies using self-report do not. Hartmann et al. (2024), across 129 studies, organized the same split quantitatively: homophily-based and computational-social-science studies tend to support it, while content-exposure and survey-based studies tend to disconfirm it.

Moving Exposure Did Not Move Attitudes

Four studies conducted on Meta’s data around the 2020 U.S. presidential election produced the strongest evidence on this point.

Nyhan et al. (2023, Nature) confirmed that 50.4% of the content visible on Facebook came from like-minded sources and 14.7% was cross-cutting, and then experimentally reduced exposure to like-minded content. No significant effect appeared on either affective polarization or beliefs.

In Guess et al.’s (2023, Science) reshare-removal experiment, exposure to political news and to untrustworthy sources fell substantially, and political knowledge dropped too, but no detectable effect appeared on beliefs or opinions. In the same team’s reverse-chronological feed experiment, usage time and the content of exposure changed substantially, yet neither issue polarization nor affective polarization moved.

Two things can be read from this. One is that the effect of an intervention that redistributes exposure is small. The other is that what such an intervention manipulates is always “which of the real human opinions that exist becomes visible.”

The remedies carry the same structure. Increasing cross-cutting exposure, bridging algorithms, and feed diversification are all interventions that change the allocation of content, on the premise that what is being supplied is the utterance of a real human being.

A Second Lineage: Misestimating Composition Ratios

There is also a body of research that has directly measured estimates of “what percentage.”

Ahler and Sood (2018) showed that respondents estimate the share of LGBT people among Democratic supporters at 32%. The actual figure is 6%. The share of high earners among Republican supporters was estimated at 38%. The actual figure is 2%. They confirmed experimentally that this error is due to neither expressive responding, nor unfamiliarity with numbers, nor ignorance of the base rate.

Nadeau, Niemi, and Levine (1993) measured overestimation of the Black, Hispanic, and Jewish population shares in a national sample, and Herda (2010) confirmed the same tendency for immigrant populations across 21 European countries.

Here too, the locus of the cause is contested. Ahler and Sood (2023) locate it in stereotype exaggeration driven by the representativeness heuristic. Guay et al. (2025, PNAS) proposed “rescaling under uncertainty,” arguing that because people, when estimating a ratio, pull their judgment toward a prior expectation near 0.5, small groups are systematically overestimated. This is a claim about a topic-independent, domain-general mechanism. Kardosh et al. (2022, PNAS), across 12 experiments with 942 participants, showed that minority faces receive prioritized processing in perception and memory, but Gayet et al. (2022) countered that the same effect can be explained by visual properties unrelated to social content, such as facial brightness, and is reproduced even with gray circles. The dispute continues as of 2026.

On the overestimation of racial composition, a scale dependence has been reported in which direct interracial contact dominates at the neighborhood scale, while the perceived frequency of news coverage dominates at the national scale.

The remedy is consistent throughout: present the true base rate. Ahler (2014) showed that an intervention presenting the actual average position of a party moderated opinion by 8% to 13%. Ahler and Sood (2023), however, also reported that even when accurate statistics are given, people with low numeracy feed them back into the representativeness heuristic as input, so the misestimation does not disappear.

The Size of the Effect

The effect size of selective exposure itself is not especially large. Hart et al.’s (2009, Psychological Bulletin) meta-analysis reports the preference for information matching one’s own attitude at d=0.36. That is a moderate effect.

Sears and Freedman (1967) were skeptical, from the outset, of the conventional view attributing attitude bias to selective exposure. An error such as estimating the LGBT share at more than five times its actual value is hard to explain by this effect size alone.

The Connection to Generative AI Already Exists

Research applying the echo-chamber framework to generative AI has also appeared. Sharma, Liao, and Xiao (2024, CHI), across two experiments, showed that LLM-based conversational search fosters more biased information seeking than conventional search, and that an LLM that agrees with the user’s opinion amplifies that bias. Jacob, Kerrigan, and Bastos (2025) compared ChatGPT with Google Search and reported a medium effect in the form of overconfidence in hallucinated content.

What Differs

Setting these side by side, three things can be distinguished.

First, where the distortion is located. What echo-chamber research addresses is a bias in the sample the observer draws. The population distribution is preserved; what is distorted, by selective exposure, homophily, or the algorithm, is which part of it becomes visible. What this note has been tracking is a different layer: how much of what is supplied corresponds to a human being at all.

Second, what the remedy presupposes. Diversifying exposure is an operation that changes the allocation of opinions that actually exist. Presenting a base rate presupposes that a true ratio exists, one that needs correcting. For an item with no corresponding human being, neither premise is satisfied, because the denominator cannot be defined.

Third, the direction of the error. In echo chambers, the distortion runs toward overestimating one’s own side’s opinion. Misestimation of composition ratios distorts toward overestimating a salient minority. Inflation of frequency through generation can run in either direction, independent of both the observer’s position and whether the group actually exists.

This third point, however, needs a qualification. If ratio estimation has the general property Guay et al. (2025) describe, of regressing toward 0.5, then the estimate is inaccurate to begin with, whatever frequency is fed into it. Contaminating the input may leave little room for the estimate to get any worse. This rebuttal holds for the task of ratio estimation. What Glickman and Sharot (2025) moved, on the other hand, is a different task, “who is typical,” where exposure does move the judgment. Which task is at stake changes the story.

What Has Been Measured, and Where the Gaps Are

Here is a summary, stated as far as possible in terms that can be asserted as fact.

The phenomenon of frequency and headcount coming apart has already been documented through at least four independent mechanisms. On the cognitive side, one person’s repetition is read as the consensus of many (Weaver et al. 2007). On the sending side, even in human-only environments, the top tenth writes eight tenths (Pew 2019; van Mierlo 2014). On the cost side, as marginal cost approaches zero, output volume becomes independent of the number of senders (Rao & Reiley 2012). On the observation side, network structure alone produces a local majority illusion (Lerman et al. 2016).

Over the last three years, three further layers have been added to this.

First, the causal path by which exposure moves the judgment of “what is normal” has now been directly demonstrated under generative-AI conditions. Glickman and Sharot’s (2025) third experiment and AlDahoul et al. (2025) establish this. As of 2024, the only material at hand was the manipulation of an artificial popularity signal, as in Salganik and Watts (2008) and Muchnik et al. (2013); now there are experiments that use the generated content itself as the stimulus. At the same time, however, reports also exist that manipulating visibility or recommendations alone produces no effect, or only a limited one (Geber & Stahel 2026; Liu et al. 2025).

Second, measurement of volume has, domain by domain, reached the point where an order of magnitude is visible. 6.5% to 16.9% in peer-review text (Liang et al. 2024); about 16% of cited sources in generative search (Allaham & Diakopoulos 2026); 10% to 30% in academic abstracts (Kobak et al. 2025); up to 9% monthly in some Reddit communities (La Cava et al. 2025).

Third, it has also been measured that the detecting side has not kept up. Watermarks have been successfully both removed and forged (Cheng et al. 2025; Wu et al. 2026; An et al. 2026); C2PA has been concluded, under independent evaluation, not to meet its stated goals (Golaszewski et al. 2026); and bot detection loses performance to LLM-based evasion (Feng et al. 2024; Dawkins et al. 2025).

Naming has already occurred too. Schroeder et al. (2026) put forward the term “synthetic consensus” in a Science policy forum. It is a proposal unaccompanied by empirical evidence, but as a concept it has arrived first.

So what remains as a gap?

Case studies of mass generation that does not require intent as a condition have begun to appear. The 7.9 million articles from pink-slime local-news sites (Horne & Gruppi 2024) are motivated by advertising revenue, and the 84 cases of agentic flooding of government services (Schmitz et al. 2026) involve no malicious actor at all. Yet the definitions of astroturfing and computational propaganda, as of 2026, still place deceptive intent at their entry point (Kovic & Rauchfleisch 2018; Woolley & Howard 2017; and likewise Mannocci et al.’s 2024 harmonizing framework). The phenomenon has begun to be described, but the definitions have not yet moved.

On detection, a lineage that judges from content alone has grown up independently (Puccetti et al. 2024; Dawkins et al. 2025). It is no longer only the lineage that uses relationships among fake personas as evidence (Kumar et al. 2017; Cresci et al. 2017; Giglietto et al. 2020; Luceri et al. 2025). Content-only detection, however, collapses substantially once an attacker merely fine-tunes a model and keeps it private.

What remained most clearly as a gap is on the measurement-theory side. Daikeler et al. (2025) systematically reviewed the 58 data-quality frameworks that existed as of 2025, and even built an evidence-gap map. What was named there as missing was visual data and linked data; an error type for the case where the sender lies outside the population is not merely absent from the frameworks, it is not even named as a gap. Newly proposed frameworks from the same period (Schneck and Przepiorka’s 2025 TEF-DBD; Jansson 2025) likewise do not anticipate a non-human sender.

Only the premise itself has been put into words, in a single instance. Alsalti, Rohrer, and Arslan (2026), in a section discussing the coverage error of the total-survey-error framework, wrote that as the use of generative AI spreads, sampling units may no longer correspond to human individuals, undermining the premise that an online sample represents a human population. This, however, is a remark of one or two sentences, and it is not formalized as a subtype of coverage error, sampling error, nonresponse error, or weighting error.

In an adjacent domain, the same statement has already been made public. Westwood (2025) stated in PNAS that the premise “a consistent response is a human response” can no longer be sustained. Its object, however, is a closed measurement apparatus with a roster, where the problem takes the form of detecting an intruder. That is a different shape of problem from trace data, which has no mechanism of its own for identifying the sender.

What can be said is that, as of August 2026, no framework structuring the case where the sender lies outside the population as an error type is to be found among the 303 sources in this collection.

The same shape of gap holds for echo chamber research, the closest neighboring concept, as well. The locus of the cause is contested across studies, but the premise that a human being stands behind each observed item is shared, and has never once been made explicit. Every remedy either changes the allocation of opinions that actually exist or presents a true ratio. Neither has a foothold for application to an item with no corresponding human being.

One rebuttal, however, applies here. If ratio estimation has the general property Guay et al. (2025) describe, of regressing toward 0.5, then the estimate is off to begin with, whatever frequency is fed into it, however inaccurate. Contaminating the input may leave less room for the estimate to worsen than it seems. For the task of ratio estimation, this rebuttal holds.

  • ai-slop-design-creativity — Reading AI slop as outsourced verification labor
  • slop-countermeasures-history — A history of countermeasures against low-quality output that have repeatedly broken down
  • slop-design-history — How the design profession was institutionalized as the first countermeasure to slop
  • Slop-era information environment (unpublished) — Examining design that does not bet on the ability to discriminate
  • ai-research-gaps-abduction — A method for gap analysis through the leap of a frame
  • Turning frequency-cue signal validity into a paper (unpublished) — The novelty verdict built on this note

References

Frequency Cues and Social Prevalence Estimation

Representation Frequency and Actual Population Ratios

High-Volume Output by Few Actors and Fabricated Majorities

The Generative-AI-Specific Information Environment

Self-Fulfillment and Norm Dynamics

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  • Biggs, M. (2009). Self-fulfilling prophecies. In The Oxford Handbook of Analytical Sociology (pp. 294–314). https://doi.org/10.1093/oxfordhb/9780199215362.013.13
  • MacKenzie, D., & Millo, Y. (2003). Constructing a market, performing theory. American Journal of Sociology, 109(1), 107–145. https://doi.org/10.1086/374404
  • MacKenzie, D. (2006). An engine, not a camera. MIT Press.
  • Marti, E., & Gond, J.-P. (2019). How do theories become self-fulfilling? Academy of Management Review, 44(3), 686–694. https://doi.org/10.5465/amr.2019.0024
  • Salganik, M. J., Dodds, P. S., & Watts, D. J. (2006). Experimental study of inequality and unpredictability in an artificial cultural market. Science, 311(5762), 854–856. https://doi.org/10.1126/science.1121066
  • Salganik, M. J., & Watts, D. J. (2008). Leading the herd astray. Social Psychology Quarterly, 71(4), 338–355. https://doi.org/10.1177/019027250807100404
  • Muchnik, L., Aral, S., & Taylor, S. J. (2013). Social influence bias: A randomized experiment. Science, 341(6146), 647–651. https://doi.org/10.1126/science.1240466
  • Bikhchandani, S., Hirshleifer, D., & Welch, I. (1992). A theory of fads, fashion, custom, and cultural change as informational cascades. Journal of Political Economy, 100(5), 992–1026. https://doi.org/10.1086/261849
  • Banerjee, A. V. (1992). A simple model of herd behavior. Quarterly Journal of Economics, 107(3), 797–817. https://doi.org/10.2307/2118364
  • Anderson, L. R., & Holt, C. A. (1997). Information cascades in the laboratory. American Economic Review, 87(5), 847–862.
  • Bicchieri, C. (2006). The grammar of society. Cambridge University Press.
  • Bicchieri, C. (2017). Norms in the wild. Oxford University Press.
  • Kuran, T. (1995). Private truths, public lies. Harvard University Press.
  • Willer, R., Kuwabara, K., & Macy, M. W. (2009). The false enforcement of unpopular norms. American Journal of Sociology, 115(2), 451–490. https://doi.org/10.1086/599250
  • Centola, D., & Baronchelli, A. (2015). The spontaneous emergence of conventions. PNAS, 112(7), 1989–1994. https://doi.org/10.1073/pnas.1418838112
  • Centola, D., Becker, J., Brackbill, D., & Baronchelli, A. (2018). Experimental evidence for tipping points in social convention. Science, 360(6393), 1116–1119. https://doi.org/10.1126/science.aas8827
  • Hacking, I. (1986). Making up people. In Reconstructing individualism (pp. 222–236). Stanford University Press.
  • Hacking, I. (1995). The looping effects of human kinds. In Causal cognition. Clarendon Press.
  • Bowles, S. (1998). Endogenous preferences. Journal of Economic Literature, 36(1), 75–111. https://sites.santafe.edu/~bowles/1998JEL.pdf
  • Slovic, P. (1995). The construction of preference. American Psychologist, 50(5), 364–371. https://doi.org/10.1037/0003-066X.50.5.364

Representativeness of Digital Trace Data

Additions from the last three years (2023–2026)

Volume measurement and detection

  • Liang, W., Izzo, Z., Zhang, Y., et al. (2024). Monitoring AI-modified content at scale: A case study on the impact of ChatGPT on AI conference peer reviews. ICML 2024. https://arxiv.org/abs/2403.07183
  • Rao, V. S., Kumar, A., Lakkaraju, H., & Shah, N. B. (2025). Detecting LLM-generated peer reviews. PLoS One. https://pmc.ncbi.nlm.nih.gov/articles/PMC12453209/
  • Liu, J., He, Y., Zheng, Z., Bu, Y., & Ni, C. (2025). AI-assisted writing is growing fastest among non-English-speaking and less established scientists. arXiv:2511.15872. https://arxiv.org/abs/2511.15872
  • Spennemann, D. H. R. (2025). Delving into: The quantification of AI-generated content on the internet. arXiv:2504.08755. https://arxiv.org/abs/2504.08755
  • Allaham, M., & Diakopoulos, N. (2026). Synthetic sources? Auditing generative search engine citations for evidence of AI-generated sources. arXiv:2605.23684. https://arxiv.org/abs/2605.23684
  • Grossman, R., Liu, S., Chen, M. K., Smith, M., Borcea, C., & Chen, Y. (2026). How generative AI disrupts search. ACM SIGIR 2026. https://arxiv.org/abs/2604.27790
  • Huang, M., Goyal, A., Saha, K., & Chandrasekharan, E. (2026). Answer bubbles: Information exposure in AI-mediated search. arXiv:2603.16138. https://arxiv.org/abs/2603.16138
  • Musser, M. (2023). A cost analysis of generative language models and influence operations. arXiv:2308.03740. https://arxiv.org/abs/2308.03740
  • Horne, B. D., & Gruppi, M. (2024). NELA-PS: A dataset of pink slime news articles for the study of local news ecosystems. ICWSM 2024. https://ojs.aaai.org/index.php/ICWSM/article/view/31439
  • Schmitz, C., Hammond, L., & Chan, A. (2026). Characterizing agentic flooding of government services. arXiv:2608.16603. https://arxiv.org/abs/2608.16603
  • Liang, W., Yuksekgonul, M., Mao, Y., Wu, E., & Zou, J. (2023). GPT detectors are biased against non-native English writers. Patterns. https://arxiv.org/abs/2304.02819
  • Al Ali, A., Helcl, J., & Libovický, J. (2026). Different time, different language: Revisiting the bias against non-native speakers in GPT detectors. arXiv:2602.05769. https://arxiv.org/abs/2602.05769
  • Cheng, Y., Guo, H., Li, Y., & Sigal, L. (2025). Revealing weaknesses in text watermarking through self-information rewrite attacks. arXiv:2505.05190. https://arxiv.org/abs/2505.05190
  • Wu, Z., Gong, G., Zhu, Q., Chen, Y., & Zhao, R. (2026). Linear ensembles wash away watermarks. arXiv:2605.30501. https://arxiv.org/abs/2605.30501
  • An, H., Park, S., Woo, S., & Han, Y.-S. (2026). DITTO: A spoofing attack framework on watermarked LLMs via knowledge distillation. EACL 2026. https://arxiv.org/abs/2510.10987
  • Golaszewski, E., et al. (2026). Verifying provenance of digital media: Why the C2PA specifications fall short. arXiv:2604.24890. https://arxiv.org/abs/2604.24890
  • Feng, S., Wan, H., Wang, N., Tan, Z., Luo, M., & Tsvetkov, Y. (2024). What does the bot say? Opportunities and risks of large language models in social media bot detection. arXiv:2402.00371. https://arxiv.org/abs/2402.00371
  • Dawkins, H., Fraser, K. C., & Kiritchenko, S. (2025). When detection fails: The power of fine-tuned models to generate human-like social media text. arXiv:2506.09975. https://arxiv.org/abs/2506.09975
  • Puccetti, G., Rogers, A., Alzetta, C., Dell’Orletta, F., & Esuli, A. (2024). AI “news” content farms are easy to make and hard to detect: A case study in Italian. arXiv:2406.12128. https://arxiv.org/abs/2406.12128
  • Mannocci, L., Mazza, M., Monreale, A., Tesconi, M., & Cresci, S. (2024). Detection and characterization of coordinated online behavior: A survey. arXiv:2408.01257. https://arxiv.org/abs/2408.01257
  • Luceri, L., Salkar, T. V., Balasubramanian, A., Pinto, G., Sun, C., & Ferrara, E. (2025). Coordinated inauthentic behavior on TikTok. arXiv:2505.10867. https://arxiv.org/abs/2505.10867

Exposure and norm perception

Measurement instruments

Differential Verification Against Echo Chamber Research

Echo Chambers and Filter Bubbles

Misestimation of Composition Ratios and Selective Exposure

Unverified Items

Some bibliographic entries could not be confirmed against their primary source page. A full list has been kept on the corpus side (source/review/representation-population-decoupling/papers.md). The following, among items discussed in the body text, apply.

  • Salganik et al. (2006) and Muchnik et al. (2013): since science.org rejects automated retrieval, the bibliographic details and abstract were cross-checked against independent sources, including PubMed, university mirrors, and the authors’ own writeups. Direct access to the full text was not obtained. [primary source unverified]
  • Shumailov et al. (2024): since the Nature full text sits behind an authentication wall, it was cross-checked against the abstract and PubMed. Numerical details within the body text remain unconfirmed. [primary source unverified]
  • La Cava et al. (2025): the venue of publication could not be confirmed on the primary page (content was confirmed via the arXiv version). [primary source unverified]
  • Metaxas et al. (2011), Hecht & Stephens (2014), Diaz et al. (2016), González-Bailón et al. (2014), Broniatowski et al. (2013): the primary URL or formal DOI remains unconfirmed for these. [primary source unverified]
  • Lazer et al. (2009, 2021): the full list of co-authors could not be confirmed. [primary source unverified]
  • Excluded: GLAAD’s annual report (a non-peer-reviewed industry-group report), and a figure, “the top 25% produce 97% of all tweets,” for which no primary source could be identified.

In the additional collection from the last three years, the share of pre-peer-review preprints (arXiv) is high. Items whose formal venue of publication could not be confirmed were marked [primary source unverified] in the corpus and distinguished from peer-reviewed literature. Among items discussed in the body text, the following apply.

  • Grossman et al. (2026), An et al. (2026), Goanta et al. (2026): conference acceptance could not be confirmed on the primary page. [primary source unverified]
  • Spennemann (2025), Liu et al. (2025), Allaham & Diakopoulos (2026), Huang et al. (2026), Cheng et al. (2025), Wu et al. (2026), Golaszewski et al. (2026), Feng et al. (2024), Dawkins et al. (2025), Puccetti et al. (2024), Schmitz et al. (2026), Ma et al. (2026), Kim et al. (2025), Murtfeldt et al. (2024): these are arXiv preprints and have not gone through peer review. [primary source unverified]
  • Horne & Gruppi (2024): the ICWSM volume and issue could not be confirmed against a primary PDF. [primary source unverified]
  • NORC (2026): the organization was confirmed, but an individual author could not be identified. [primary source unverified]
  • Jansson (2025), Weiß et al. (2025): the full text could not be retrieved, so whether it discusses non-human senders could not be confirmed. [primary source unverified]
  • Excluded: web-wide AI-generation ratios estimated by detection vendors using their own detectors (Graphite, Pangram, Originality.ai); Adobe Stock’s ratio, whose methodology is undisclosed; and Indeed’s job-posting estimate, whose transformation-index definition is undisclosed. All were recorded in the corpus as the source’s own claim but are not cited in the body text as fact.
  • The unauthorized LLM persuasion experiment itself on Reddit’s r/changemyview in 2025 lacks identified authors and affiliation and was not peer-reviewed, so the experiment report itself is not included in the corpus. Only the subsequent academic secondary analysis (Jaidka & Ahmed 2026, a preprint) was recorded.

Among the 51 sources added in the differential check against echo chamber research, primary confirmation could not be obtained for the following.

  • Arguedas et al. (2022): the DOI notation is only an inference from Reuters Institute convention. Reaching the publication page itself has been confirmed. [primary source unverified]
  • González-Bailón et al. (2023): the specific figures for the relative contribution of algorithmic selection versus engagement could not be confirmed. [primary source unverified]
  • Sunstein (2001): the publisher’s bibliographic page could not be reached; confirmed via a university repository mirror instead. [primary source unverified]
  • Guay et al. (2026), and the related PNAS reply: the body text sits behind a paywall, so content could not be confirmed. [primary source unverified]
  • Kardosh et al. (2022): the specific magnitude of the overestimation could not be confirmed from the abstract alone. [primary source unverified]
  • Karimi et al. (2017), Miller & McFarland (1987): the formal venue of publication and DOI could not be confirmed. [primary source unverified]
  • Eminente et al. (2026): an arXiv preprint that has not gone through peer review. [primary source unverified]

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