Does Generative AI Raise University Students' Motivation and Engagement? Reading the Meta-Analysis by Xia et al. (2025)

What the paper claims

Xia, Li, Yang, Weng, and Chiu (2025) report a meta-analysis that concludes that generative AI raises university students’ motivation and engagement. The authors collected experiments and quasi-experiments published in or after November 2022 that compared a group using generative AI with a group that did not, and that measured motivation or engagement. The search ended on September 30, 2024, and 33 studies were included from 2,059 database records and 20 studies found through citation tracking. Effect sizes were computed as Hedges’ g and pooled with a random-effects model.

All reported effects were positive and significant. For motivation, g = 1.20 (12 studies, 1,099 students); for cognitive engagement, 0.59 (25 studies, 2,571 students); for behavioral engagement, 0.52 (12 studies, 830 students); for emotional engagement, 0.64 (13 studies, 1,365 students); and for agency engagement, 0.87 (5 studies, 651 students). The four types of engagement follow the frameworks of Fredricks and colleagues and of Reeve and Tseng. In the abstract, the authors further state that subject, learning strategy (individual or collaborative), and context of use (in class, outside class, or both) moderate the effects. They add that individual and small-group learning and the use of ChatGPT are especially effective, and in the discussion they state that teachers and students should embrace generative AI.

The motivation effect of g = 1.20 is large compared with other meta-analyses from the same period. The abstract of Liu et al. (2025, 49 studies), which pooled learning outcomes and motivation separately, reports 0.803 for motivation, and Doo and Park (2026, 86 studies), who divided the learning outcomes of ChatGPT into affective, cognitive, and metacognitive domains, report g = 0.481 for the affective domain, which includes motivation and emotional engagement.

Did the 33 studies compare generative AI?

The eligibility criteria require publication in or after November 2022 (a cutoff aligned with the release of ChatGPT) and a comparison between a group that used generative AI and a group that did not. However, the included studies contain tools that do not generate text and a study published before the cutoff.

Han, Park, and Lee (2022) conducted a quasi-experiment with 61 nursing students and collected the data from November 3 to 16, 2021. Their chatbot recognized the intent and entities of a user’s question through natural language processing and then selected the most suitable answer from a database of accumulated answers; it did not generate text. The Smart Sender platform that Nozhovnik et al. (2023) used in foreign language classes is a chatbot builder with which non-technical users construct conversation scenarios, and it was combined with gamification to automate the classes. Lee, Hwang, and Chen (2022) was published online on August 1, 2022, according to the Crossref record, which is before the publication cutoff. Xia et al. classified all three studies as educational chatbots and included Lee et al. and Nozhovnik et al. in the motivation analysis.

The coding of tool type also contains a misclassification. Sun et al. (2024) examined a programming course that used ChatGPT, as the title states, but the overview table of Xia et al. lists the study as an educational chatbot. For motivation, educational chatbots showed g = 1.73 (6 studies) and ChatGPT showed 0.71 (6 studies), and the difference was not significant (p = 0.09). The number reported as the effect of generative AI therefore mixes in studies of tools that do not generate text, and the paper gives no estimate that separates them.

The control conditions also differ. The criteria only require a group that did not use generative AI, and what that group did is not among the six coded variables (sample size, duration, subject, learning strategy, context of use, and tool type). In Han et al., the control group watched a video lecture only, while the experimental group watched the same video and also took a chatbot lesson, so the experimental group had more opportunities to learn. In Essel et al. (2024), the control group performed the same tasks with conventional databases and search engines (abstract). In Escalante et al. (2023), the control group received feedback from a human tutor, and writing scores over six weeks did not differ between groups. When control groups that receive nothing are pooled with control groups that receive another form of support, the pooled mean combines the effect of the tool, the effect of added activity, and the effect of different instructional methods without separating them.

This problem has been counted directly in other ChatGPT meta-analyses from the same period. Lawson et al. (2026) coded the primary studies of Deng et al. (2025) and of Wang and Fan (2025, later retracted) for whether the groups were matched on instructional methods, practice with the dependent measure, and learning time. Of the 27 comparisons in Deng et al. in which the ChatGPT group performed significantly better, only one (3.70%) could be judged comparable, 11 were not comparable, and 15 could not be judged because information was missing. Among the comparisons with unmatched instructional methods, almost all differences favored the ChatGPT group (for example, only the ChatGPT group received feedback or problem-solving support). Weidlich, Gašević, Drachsler, and Kirschner (2025) used the same analysis by Deng et al. as an example and argued that interpreting such effects requires three considerations: the precise nature of the treatment, the activities of the control group, and the validity of the outcome measures as indicators of learning. The coding of Xia et al. stops at tool type and does not address what students did in the treatment, what the control groups did, or whether the motivation and engagement measures are valid indicators of learning.

What was measured?

What the paper calls motivation and engagement does not refer to a single kind of measure. Xia et al. define cognitive engagement as the intellectual effort that students put into learning, reflected in self-efficacy, learning goals, and self-regulation. Under this definition, an increase in self-efficacy counts as an increase in cognitive engagement. As a result, a study in which intellectual effort decreased can still be read as showing higher cognitive engagement. In the experiment by Urban et al. (2024), which Xia et al. placed in both the cognitive and emotional categories, students who used ChatGPT reported higher self-efficacy for the task (d = 0.65) and produced better solutions. However, they also perceived the task as easier, reported less mental effort (d = 0.58), and did not find the task more interesting (d = 0.08). The text of Xia et al. does not show which value was extracted from this study.

The treatment of agency engagement also shows a gap between definition and example. As cited by Xia et al., agency engagement in Reeve and Tseng (2011) refers to students’ constructive contribution to the flow of the instruction they receive. Xia et al. present a study in which ChatGPT-assisted reading increased students’ willingness to continue reading as an example of improved agency engagement. Willingness to continue reading is different from acting on the flow of instruction. The studies classified under behavioral engagement include a study whose group comparison was writing scores, such as Escalante et al., and a study that counted logged actions, such as Sun et al. In the logs of Sun et al., the ChatGPT group debugged and read error messages more often, but it also copied and pasted code from ChatGPT more often, and the groups did not differ significantly in performance. A higher count of actions alone does not show deeper involvement in learning.

Most measures are self-reports. Within the full texts checked, Nozhovnik et al. used researcher-designed questionnaires on motivation and engagement, and Song and Song (2023) used questionnaires and interviews. Weidlich et al. point out that in Hu (2024), which Xia et al. also included, the measures were self-ratings of problem-solving skills and ethical reasoning ability and self-reports of motivational regulation, so that higher-order thinking was “stated but not demonstrated.” In contrast, the MERSQI table that Xia et al. used for quality appraisal counts 29 of the 33 studies as using objective measurement and 29 as having knowledge and skills as outcomes. This count does not match the number of studies that measured motivation with questionnaires. The mean quality score of 12.85 can be read as a rating of the measures for each study’s main learning outcome rather than of the motivation and engagement measures that the meta-analysis pooled.

Other experiments show that self-reports can diverge from the amount learned. Deslauriers et al. (2019) randomly assigned 149 students in an introductory physics course to active instruction or passive lectures and found that students in active instruction scored about 0.46 standard deviations higher on a test but reported a feeling of learning about 0.56 standard deviations lower. Ways of learning that require effort can lower the feeling of having learned. If self-reported motivation and engagement are used as indicators of effect, this opposite relation is missed.

How stable are the numbers?

The first concern in the statistical treatment is that overall heterogeneity is not reported. Although the paper states that it used a random-effects model, none of the five pooled results is accompanied in the text or tables by Q, I², τ², or a prediction interval, which would show the spread between studies. The forest plots are images, and whether they contain these values was not checked. The moderator tables nonetheless show a large spread. When motivation is divided by context of use, the three studies that used the tool in class only show g = 2.94, the five studies outside class only show 0.84, and the four studies with mixed use show 0.44. The three in-class studies are Wang et al. (2024), Nozhovnik et al. (2023), and Hu (2024), which include the study of a scripted chatbot and the study whose self-report measures Weidlich et al. criticized. When the effects are recalculated from the published data, the nine studies without these three have a mean of 0.58, so the overall value of 1.20 is pulled strongly by these three studies. In a ChatGPT meta-analysis from the same period, Doo and Park (2026) report I² = 83.37% and a prediction interval from −0.47 to 1.61, a spread wide enough to allow a negative effect in the next study.

Many moderator analyses rest on a few studies. Collaborative learning is represented by one study for motivation (g = 0.07) and one study for emotional engagement, and studies with more than 100 participants are represented by one study for behavioral engagement (g = −0.06). The authors acknowledge in their limitations that the uneven number of studies across categories may affect the robustness of the moderator analysis.

The treatment of publication bias is also too weak to support the conclusion that no bias exists. The authors judged that there was no bias on the basis of funnel plots, fail-safe N, and Egger’s regression. However, the one-tailed p-values of Egger’s test were 0.08 for cognitive engagement and 0.06 for behavioral engagement, and the two-tailed p-value for motivation was 0.09, all close to the threshold. The paper cites the trim-and-fill literature but reports no adjusted estimates. Ropovik et al. (2021), who examined 110 meta-analyses in education, found that only four (4%) based their conclusions on bias-adjusted estimates, and the treatment by Xia et al. falls within this majority. The tables also show a tendency for smaller studies to have larger effects. For cognitive engagement, studies with 100 or fewer participants show 0.69 and larger studies show 0.42; for emotional engagement, the values are 0.76 and 0.37; the differences were not significant, but the direction is consistent. The abstract of Cheung and Slavin (2016) reports that, across 645 evaluation studies in education, small-scale trials and experimenter-made measures produced effect sizes roughly twice as large as large-scale trials and independent measures. Bartoš et al. (2026, a preprint not peer reviewed), who pooled 1,840 effect sizes from 67 meta-analyses of AI and learning and included the paper by Xia et al., report that adjusting for publication bias reduces the mean effect to about one-third of the unadjusted value (SMD = 0.196) and widens the prediction interval to −1.521 to 1.908.

The association rule analysis adds little new information. Using the Apriori algorithm, Xia et al. extracted rules such as “individual learning and small groups lead to a positive direction of the motivation effect” and, on the basis of a confidence of 1 and a lift of 1.10, wrote that individual learning increases motivation “significantly.” Because lift is the confidence divided by the base rate of the conclusion, a confidence of 1 with a lift of 1.10 means that about 0.91 of all effects were positive. These rules therefore come close to restating, for each combination of conditions, the fact that most studies reported positive effects. The support of the rules ranges from 0.10 to 0.19, so each rule rests on a small number of effects.

What changes when the published data are recalculated?

Xia et al. published the numbers behind their effect sizes on figshare (CC BY 4.0). We recalculated the effect sizes from the sheet in that Excel file that codes each included study by category. For studies with pre-test and post-test scores, the difference in change between groups was divided by the pooled post-test standard deviation, and the effects were pooled with a random-effects model (REML). With this procedure, motivation was 1.17 (1.20 in the paper), cognitive engagement was 0.59 (0.59), and emotional engagement was 0.63 (0.64); the three in-class studies gave 2.93 (2.94), and the six educational chatbot studies gave 1.73 (1.73). Behavioural engagement (0.44 against 0.52) and agentic engagement (0.57 against 0.87) were not reproduced, and the details of the paper’s calculation, such as how the pre-post correlation was handled, cannot be read from the text. The procedure, scripts, and output are kept in the corpus.

The variation between studies is large. I² was 93% for motivation, 91% for cognitive, 87% for behavioural, 85% for emotional, and 90% for agentic engagement. The 95% prediction intervals were −1.55 to 3.89 for motivation, −1.19 to 2.38 for cognitive, and −0.80 to 2.06 for emotional engagement, and the interval for every category includes negative values. A prediction interval shows the range in which the effect of one new study under similar conditions may fall. Therefore, even though the mean is positive and significant, a class in which the group using generative AI reports lower motivation is within the range of this result.

Removing the tools that do not generate text and the study published before the cutoff changes the numbers only a little. Without Han et al., Nozhovnik et al., and Lee et al., motivation was 0.96 (10 studies), cognitive engagement was 0.56, and emotional engagement was 0.63. The large motivation mean depends more on the three in-class studies than on the type of tool.

When the tendency of smaller studies to show larger effects is corrected by regression (the PET intercept), motivation becomes −0.10, cognitive engagement −0.07, and emotional engagement 0.08. However, with 12 to 25 studies and this much variation, the corrected estimate is unstable. In addition to publication bias, larger effects in small studies can arise from researcher-made measures and differences in design (as the abstract of Cheung and Slavin reports). This result does not show that the true effect is zero. What it shows is that the possibility that the positive mean rests on small studies cannot be excluded, which is in the same direction as the correction by Bartoš et al. that reduced the mean to about one third.

The data also contain a copying error. For the clinical reasoning competency of Han et al., the sheet gives the post-test mean and standard deviation of the control group as 11.90 and 6.91. These are the change score (post-test minus pre-test) of the experimental group in the original table, and the post-test values of the control group are 58.97 and 8.74. The original paper reports no significant group difference in either knowledge or clinical reasoning competency (p = .567 and p = .455). With the correct values, the cognitive effect of Han et al. changes from 1.27 to −0.02, and the pooled cognitive effect falls from 0.59 to 0.54.

Some exclusions are not described in the text. In the notes column of the sheet, six rows are marked “exclude” with the reason “publication bias”. They are the overall writing score of Boudouaia et al. (2024), the cognitive and behavioural outcomes of Nozhovnik et al., the emotional outcome of Wahba et al. (2024), and the cognitive and emotional outcomes of Ododo et al. (2024). The text describes only the exclusion of the overall score of Boudouaia et al., whose effect size was judged large enough to distort the adjustment for publication bias, and Ododo et al. do not appear in the text or in the list of 33 studies. The six rows have effect sizes from 3.72 to 11.43, and restoring them raises cognitive engagement to 0.88, behavioural engagement to 0.98, and emotional engagement to 1.24. These exclusions lowered the reported values. However, removing large effects is not a method for correcting publication bias. Because the text does not say which rows were removed and why, readers cannot check which decisions the reported values depend on.

Do the conclusions go beyond the tables?

Several statements in the discussion and conclusion are not supported by the moderator tables. The claim that students in science fields show larger effects on motivation and on cognitive and emotional engagement does not match the tables. For cognitive engagement, the humanities show 0.51 and science and engineering show 0.48, almost the same, and the difference between subjects comes from medicine (1.27, 6 studies). For motivation, science and engineering are represented by two studies, and for emotional engagement by one. The suggestion that specialized educational AI raises cognitive engagement more than general generative AI also rests on a non-significant difference (p = 0.20). The abstract says “especially using ChatGPT,” but the differences between ChatGPT and educational chatbots are not significant for motivation, cognitive, emotional, behavioral, or agency engagement, and the direction changes from one outcome to another. The practical recommendation that individual learning is more effective rests on comparisons with collaborative categories that contain one to five studies.

The statement that teachers and students should embrace generative AI derives an educational policy from an average increase in self-reported motivation and engagement. The paper does not pool learning outcomes and does not measure whether the effects persist (duration is coded only as four weeks or less versus more than four weeks). The paper claims as a theoretical contribution that it empirically supports existing theories of motivation and engagement, but no analysis tests a prediction derived from theory.

The journal is an open-access Elsevier journal, and according to the OpenAlex record it is listed in DOAJ and the CWTS core journal list, with no sign of a predatory journal. However, the published text retains the anonymization placeholder “Author, 2023,” and the limitations section states that only peer-reviewed English journal papers were included, although three conference papers are included; these inconsistencies were not caught during editing.

Does higher motivation and engagement mean more learning?

The paper answers whether groups that used generative AI reported higher motivation and engagement than groups that did not. Whether this leads to deeper learning or to lasting autonomous learning remains a separate question. Findings in existing notes show that the two can diverge.

Fan et al. (2025) randomly assigned university students to four conditions (ChatGPT, a human expert, writing analytics tools, and no support) and found no difference in post-task intrinsic motivation across conditions. In the same experiment, the ChatGPT group improved its essay scores the most, but there was no difference in knowledge gain and transfer, and the authors called the state in which reliance on AI leads learners to give up planning, monitoring, and evaluating their own work “metacognitive laziness.” Fan et al. was published after the search cutoff of Xia et al., so a randomized experiment outside the pooled mean found no difference in motivation. In the high school mathematics experiment by Bastani et al. (2025), students who used a GPT-4 that gave answers improved their practice grades by 48% but scored 17% lower than the control group on an exam without AI. This decline was largely mitigated in a condition designed to guide with hints instead of answers (Does Early Use of Generative AI Inhibit the Formation of Thought? A Literature Map of Cognitive Offloading and Learning). Studies of end-user development have also repeatedly reported that increases in self-efficacy do not correspond to gains in ability (Does Being Able to Build Mean Being Able to Learn? Rereading the Learning Outcomes of End-User Development Through Motive). In the experiment by Urban et al., the self-evaluations of students who used ChatGPT did not correlate with their performance, and the authors interpreted this as difficulty in calibrating self-evaluation.

The lack of distinction between types of motivation is also a gap in any argument about long-term autonomy. Self-determination theory distinguishes motivation that people endorse as their own from motivation that is externally controlled, and it holds that rewards, deadlines, pressured evaluations, and imposed goals can diminish intrinsic motivation (Ryan and Deci 2000; Scaffolding Learning and the Design of Interventions: A Literature Map of Cognitive Apprenticeship, Legitimate Peripheral Participation, and Theories of Mediation). Ryong et al. (2024), which Xia et al. included, compared a chatbot that stimulated intrinsic motivation with a chatbot that promoted extrinsic motivation, and the abstract reports that the controlling support of the latter improved the learning experience. The classes in Nozhovnik et al. combined scripted chatbot conversations with gamification. When such studies are pooled into a single mean for motivation, it becomes impossible to tell whether the increased motivation was autonomous or controlled. Xia et al. speculate that agency engagement was not moderated by context variables because it depends on intrinsic motivation, but the analysis contains no measure that could test this.

Does the effect support trying and trying again?

From the view that design should create environments where people can try and try again, the question is whether generative AI increased learners’ attempts or shortened them by providing evaluations and correct answers. The paper by Xia et al. lacks the variables needed to answer this question. The six coded variables are sample size, duration, subject, learning strategy, context of use, and tool type. The paper does not code whether the AI handed over answers or returned hints and questions, whether learners attempted the task before asking the AI, how many times they revised in response to the AI, or what was measured after the AI was removed.

The included studies contain both types. In Escalante et al., GPT-4 feedback on the essays that students wrote each week arrived within two working days so that students could use it in their revisions. This design uses the AI to run a cycle of attempting and then revising. In Sun et al., the ChatGPT group debugged and read error messages more often, but it also copied and pasted code from ChatGPT more often. The chatbot in Han et al. returned answers from a database in response to questions. The students in Urban et al. perceived the task as easier and reported less mental effort. When these studies are pooled into one mean, the effects of uses that support attempts and uses that skip them either cancel each other out or add together.

The increase in emotional engagement is especially ambiguous. The abstract of Yin et al. (2024) reports that chatbot-based formative feedback increased learning interest and perceived choice and decreased perceived pressure and cognitive load. Lower pressure and load make the task easier to take up. On the other hand, research on learning from failure has shown that experiencing an impasse before being taught the canonical solution deepens learning, and that this effect depends on the quality of the consolidation after failure (Designing Failure Into Learning: From Expectation Failure to Productive Failure and Industry Implementations). In the literature on junior skill formation, using AI to request explanations after first attempting a task oneself also maintained or improved understanding (What Should Juniors Do When Generative AI Takes Away the Entry-Level Work? (Academic Research)). Higher self-reported enjoyment and lower burden can therefore be evidence that attempts through impasses increased, or evidence that the impasses disappeared. Which of these occurred cannot be determined unless the type of AI response and the order of attempts are coded.

Judged from this view, the effects in the paper show an increase in self-reported motivation and engagement, but the design of the paper cannot show whether this increase resulted from support for trying and trying again. Answering that question would require studies of the following kind. They would compare a condition in which the AI hands over answers with a condition in which it returns questions or feedback, using the same tasks and the same learning time. They would also record the number of independent attempts and revisions and measure outcomes on a delayed test after the AI is removed, alongside self-reported motivation.

What the paper can and cannot support

The paper can support the claim that, in studies of higher education published in English up to September 2024, groups that used chatbots or generative AI reported higher motivation and engagement on average than comparison groups. The interventions were short, most measures were self-reports, and the size of the effect varied greatly between studies (I² from 85% to 93%).

The paper cannot support the claims that the effect is specific to generative AI or that it arises from the tool rather than from added activity or different instructional methods. Nor can it support the claims that the effect lasts, that it leads to learning outcomes or autonomous learning, or that it is especially large in science fields or in individual learning. The motivation effect of g = 1.20 is best read as a mean pulled strongly by the three in-class studies, and its prediction interval includes the case in which the next study finds a negative effect.

The paper agrees with existing findings in that the effect varies greatly with how and where the tool is used. This points in the same direction as the lesson of the assistance dilemma, in which the amount and design of support separate harm from benefit (Does Early Use of Generative AI Inhibit the Formation of Thought? A Literature Map of Cognitive Offloading and Learning). The paper diverges from existing findings in that it equates higher motivation and engagement with improved learning, whereas randomized experiments show cases in which motivation does not differ and cases in which scores rise without gains in understanding.

Related notes

• Does Early Use of Generative AI Inhibit the Formation of Thought? A Literature Map of Cognitive Offloading and Learning: Early use of generative AI, the development of thinking, and cognitive offloading
• Research Currents in AI, Education, and the Learning Sciences: Evidence on Generative AI and Learning (2024–2026): Trends in empirical research on generative AI and learning (agreement among meta-analyses and a retraction)
• Designing Failure Into Learning: From Expectation Failure to Productive Failure and Industry Implementations: Learning designs that use intentional failure
• What Should Juniors Do When Generative AI Takes Away the Entry-Level Work? (Academic Research): What juniors can do when entry-level work decreases
• Does Being Able to Build Mean Being Able to Learn? Rereading the Learning Outcomes of End-User Development Through Motive: Making and learning, self-efficacy and ability
• Scaffolding Learning and the Design of Interventions: A Literature Map of Cognitive Apprenticeship, Legitimate Peripheral Participation, and Theories of Mediation: Scaffolding, fading, and self-determination theory
• Novice Group Work with a Shared AI Agent: A Literature Map of CSCL and AI-Supported Collaborative Learning (2026): Group work and shared AI agents

Unverified items

No main claim relies on unverified material. The following peripheral statements were written within the scope of abstracts because the full texts could not be reached: the motivation effect size in Liu et al. (2025), the ratio of effect sizes in Cheung and Slavin (2016), the control condition in Essel et al. (2024), and the results of Ryong et al. (2024) and Yin et al. (2024). For these papers, the publisher pages refused access, and no open-access copy was found. The forest plots and funnel plots in Xia et al. are images, and whether they contain heterogeneity statistics was not checked (heterogeneity was recalculated from the published data). The recalculation did not reproduce agentic engagement (0.87) or behavioural engagement (0.52), so the recalculated values for these two categories may differ from the paper’s procedure.

References

All sources accessed 2026-10-24. The ledger and verification records are in source/review/genai-motivation-engagement-meta-analysis/papers.md.

Target paper

• Xia, Qi, Weijia Li, Yiming Yang, Xiaojing Weng, and Thomas K. F. Chiu. 2025. “A Systematic Review and Meta-Analysis of the Effectiveness of Generative Artificial Intelligence (GenAI) on Students’ Motivation and Engagement.” Computers and Education: Artificial Intelligence 9: 100455. https://doi.org/10.1016/j.caeai.2025.100455

• (Dataset) “A Systematic Review and Meta-Analysis of the Effectiveness of Generative Artificial Intelligence (GenAI) on Students’ Motivation and Engagement.” figshare (published data for Xia et al. 2025, CC BY 4.0). https://figshare.com/s/e278c289547d2d81011b

Studies included in the target paper

• Escalante, Juan, Austin Pack, and Alex Barrett. 2023. “AI-Generated Feedback on Writing: Insights into Efficacy and ENL Student Preference.” International Journal of Educational Technology in Higher Education 20: 57. https://doi.org/10.1186/s41239-023-00425-2
• Essel, Harry Barton, Dimitrios Vlachopoulos, Albert Benjamin Essuman, and John Opuni Amankwa. 2024. “ChatGPT Effects on Cognitive Skills of Undergraduate Students: Receiving Instant Responses from AI-Based Conversational Large Language Models (LLMs).” Computers and Education: Artificial Intelligence 6: 100198. https://doi.org/10.1016/j.caeai.2023.100198
• Han, Jeong-Won, Junhee Park, and Hanna Lee. 2022. “Analysis of the Effect of an Artificial Intelligence Chatbot Educational Program on Non-Face-to-Face Classes: A Quasi-Experimental Study.” BMC Medical Education 22: 830. https://doi.org/10.1186/s12909-022-03898-3
• Lee, Yen-Fen, Gwo-Jen Hwang, and Pei-Ying Chen. 2022. “Impacts of an AI-Based Chabot on College Students’ After-Class Review, Academic Performance, Self-Efficacy, Learning Attitude, and Motivation.” Educational Technology Research and Development 70 (5): 1843–1865. https://doi.org/10.1007/s11423-022-10142-8
• Nozhovnik, Oleh, Tetiana Harbuza, Natalia Teslenko, Olena Okhrimenko, Viktoriia Zalizniuk, and Alla Durdas. 2023. “Chatbot Gamified and Automated Management of L2 Learning Process Using Smart Sender Platform.” International Journal of Educational Methodology 9 (3): 603–618. https://doi.org/10.12973/ijem.9.3.603
• Ryong, Kyungjin, Daeho Lee, and Jae-gil Lee. 2024. “Chatbot’s Complementary Motivation Support in Developing Study Plan of E-Learning English Lecture.” International Journal of Human–Computer Interaction 40 (10): 2641–2655. https://doi.org/10.1080/10447318.2022.2163786
• Song, Cuiping, and Yanping Song. 2023. “Enhancing Academic Writing Skills and Motivation: Assessing the Efficacy of ChatGPT in AI-Assisted Language Learning for EFL Students.” Frontiers in Psychology 14: 1260843. https://doi.org/10.3389/fpsyg.2023.1260843
• Sun, Dan, Azzeddine Boudouaia, Chengcong Zhu, and Yan Li. 2024. “Would ChatGPT-Facilitated Programming Mode Impact College Students’ Programming Behaviors, Performances, and Perceptions? An Empirical Study.” International Journal of Educational Technology in Higher Education 21: 14. https://doi.org/10.1186/s41239-024-00446-5
• Urban, Marek, Filip Děchtěrenko, Jiří Lukavský, Veronika Hrabalová, Filip Svacha, Cyril Brom, and Kamila Urban. 2024. “ChatGPT Improves Creative Problem-Solving Performance in University Students: An Experimental Study.” Computers & Education 215: 105031. https://doi.org/10.1016/j.compedu.2024.105031
• Yin, Jiaqi, Tiong-Thye Goh, and Yi Hu. 2024. “Using a Chatbot to Provide Formative Feedback: A Longitudinal Study of Intrinsic Motivation, Cognitive Load, and Learning Performance.” IEEE Transactions on Learning Technologies 17: 1378–1389. https://doi.org/10.1109/tlt.2024.3364015

Other meta-analyses and methodological critiques

• Bartoš, František, Oliwia Z. Bujak, Patrícia Martinková, and Eric-Jan Wagenmakers. 2026. “Effect of Artificial Intelligence on Learning: A Meta-Meta-Analysis.” PsyArXiv (preprint, not peer reviewed). https://doi.org/10.31234/osf.io/h529e_v1
• Cheung, Alan C. K., and Robert E. Slavin. 2016. “How Methodological Features Affect Effect Sizes in Education.” Educational Researcher 45 (5): 283–292. https://doi.org/10.3102/0013189X16656615
• Doo, Min Young, and Yeonjeong Park. 2026. “A Meta-Analysis of ChatGPT’s Influence on Learning Achievement.” International Review of Research in Open and Distributed Learning 27 (1): 265–289. https://doi.org/10.19173/irrodl.v27i1.8775
• Lawson, Alyssa P., Amedee Marchand Martella, Joshua Weidlich, Miriam Mulders, and Josef Buchner. 2026. “Color Me Confounded: A Critical Analysis of Media Comparisons on ChatGPT in Education.” Computers & Education 254: 105701. https://doi.org/10.1016/j.compedu.2026.105701
• Liu, Xiaohong, Baoxin Guo, Wei He, and Xiaoyong Hu. 2025. “Effects of Generative Artificial Intelligence on K-12 and Higher Education Students’ Learning Outcomes: A Meta-Analysis.” Journal of Educational Computing Research 63 (5): 1249–1291. https://doi.org/10.1177/07356331251329185
• Ropovik, Ivan, Matus Adamkovic, and David Greger. 2021. “Neglect of Publication Bias Compromises Meta-Analyses of Educational Research.” PLOS ONE 16 (6): e0252415. https://doi.org/10.1371/journal.pone.0252415
• Weidlich, Joshua, Dragan Gašević, Hendrik Drachsler, and Paul A. Kirschner. 2025. “ChatGPT in Education: An Effect in Search of a Cause.” Journal of Computer Assisted Learning 41 (5): e70105. https://doi.org/10.1111/jcal.70105

Experiments and theory on learning and motivation

• Bastani, Hamsa, Osbert Bastani, Alp Sungu, Haosen Ge, Özge Kabakcı, and Rei Mariman. 2025. “Generative AI without Guardrails Can Harm Learning: Evidence from High School Mathematics.” Proceedings of the National Academy of Sciences 122 (26): e2422633122. https://doi.org/10.1073/pnas.2422633122
• Deslauriers, Louis, Logan S. McCarty, Kelly Miller, Kristina Callaghan, and Greg Kestin. 2019. “Measuring Actual Learning versus Feeling of Learning in Response to Being Actively Engaged in the Classroom.” Proceedings of the National Academy of Sciences 116 (39): 19251–19257. https://doi.org/10.1073/pnas.1821936116
• Fan, Yizhou, Luzhen Tang, Huixiao Le, Kejie Shen, Shufang Tan, Yueying Zhao, Yuan Shen, Xinyu Li, and Dragan Gašević. 2025. “Beware of Metacognitive Laziness: Effects of Generative Artificial Intelligence on Learning Motivation, Processes, and Performance.” British Journal of Educational Technology 56 (2): 489–530. https://doi.org/10.1111/bjet.13544
• Ryan, Richard M., and Edward L. Deci. 2000. “Self-Determination Theory and the Facilitation of Intrinsic Motivation, Social Development, and Well-Being.” American Psychologist 55 (1): 68–78. https://doi.org/10.1037/0003-066X.55.1.68