Should a Teaching Article Explain Why It Matters or Add Fun Facts? Experiments on Stating Usefulness, Writing About Usefulness, Choice, and Irrelevant Details

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This is part 14 of the series "Writing Articles That Teach," in its third section, "what readers bring with them." The first two sections covered what goes on the page (text, diagrams, code, notation and terminology, video, laying out video and text, interactivity) and what to ask readers to do (the evidence for learning by doing, questions and feedback). This post is about the reader's motivation: when an author says "here is what this is good for," lets readers pick the example they want, or adds a fun story, does any of it help, and for whom? Readers' prior knowledge and the wrong things they already believe were covered in earlier posts: writing for readers at different levels and writing the "common misconceptions" part.

The trigger was this site's writing specs. The series-planning skill has an arc principle that translates roughly as "motivation before abstraction": first let readers feel why they need something, then teach it. Harder posts open with a "scene" that uses a model behavior readers already know as the hook. Course guides also state usefulness directly. For example, the MIT 6.7960 Lecture 8 guide and six others in that series end with a section titled (in translation) "why this matters in practice." Writing those passages raises two questions. What does stating usefulness actually do for readers? And when you have an interesting story that touches the topic but plays no part in the argument, does putting it in make the article easier to read, or does it distract?

Two earlier posts on this site touched the second question. The post on questions and feedback summarized a meta-analysis on "interesting but irrelevant content" in one paragraph; the post on diagrams cited the journal version's numbers secondhand. This post reads the dissertation version of that meta-analysis in full and adds two newer sets of experiments.

How the sources were chosen and how they lean. The source list came from a literature scan followed by close reading. There are 12 references; one of them is a large-scale study that a later post on why readers don't finish will cover in detail, and this post quotes only one part of it. Each was read through in the version I could obtain, with an extraction record; what I could not read is noted in parentheses in the references. Three biases up front. First, nearly all of the usefulness research comes from one group (Judith Harackiewicz's lab at the University of Wisconsin and researchers trained there); the only two exceptions are a study of a remote course and the MOOC study. Second, the two newer sets of experiments on irrelevant details come from one German team. Third, the participants are mostly college students taking part for course credit or pay, and most tests came right after reading. Two sources could only be used in part: for Hulleman and Harackiewicz's 2009 paper in Science, I read only the supplementary materials the publisher makes public, not the main text; for Hidi and Renninger's 2006 model of interest development, I did not find a legally available full text, so this post does not cite its content.

The short version

The d and g in the table are how many standard deviations apart the two groups' averages are; a minus sign means the group with that move did worse. "Moderation" means whether the size of the effect changes with some reader characteristic (confidence, interest, prior grades).

Three terms

Usefulness (utility value) is one kind of value in expectancy-value theory: whether learning something serves your own goals. These studies manipulate it in two ways. One is stating it directly: the material or the instructor tells learners where the thing is used. The other is writing it yourself: learners write a passage about how what they learned connects to their own lives. The two are often lumped together, but the results differ, so they are treated separately below.

Interest comes in layers in these studies. Asher and Harackiewicz distinguish triggered situational interest (is this lesson engaging in the moment?) from maintained situational interest (do I want to come back to this topic itself?). The distinction comes from Hidi and Renninger's 2006 model; I did not find a legally available full text of that paper, so the description here follows how Asher and colleagues use it. The studies measure interest differently; most use self-report scales filled in right after learning.

Interesting but irrelevant details (seductive details) is a term from educational psychology: text or images that touch the topic and that readers find interesting, but that do not help them understand what the main text teaches. For example, inserting into a passage on the carbon cycle a note on which years Germany lost the most to natural disasters, with a photo of cracked dry ground (an actual example from Wesenberg and colleagues' 2025 experiments). A story or example tied directly to the question the main text answers does not fall into this category by definition.

Telling readers what it's good for

Seven experiments pooled: Asher and Harackiewicz 2025

Michael Asher and Judith Harackiewicz's 2025 study is the largest lab experiment among these sources: the same procedure was run seven times, with 2,019 college students in introductory psychology in total, and the seven results were then pooled. Everyone watched the same multiple-regression lesson content and was randomly assigned to a condition beforehand.

The direct-usefulness group first watched a roughly 3-minute video in which an instructor explained how regression is used in medicine, politics, and psychology; the control group watched a 3-minute history of regression. Results:

• The usefulness group rated regression as more useful, d = 0.41.
• No difference was detected in interest triggered by the lesson; maintained interest in regression as a topic was higher in the usefulness group, but the effect was small (d = 0.15).
• Asked after the lesson whether they wanted to leave an email address to request campus statistics resources, 39.2% of the usefulness group and 33.2% of the control group did, p = .042. Taken experiment by experiment, only one reached significance on its own.
• No difference was detected on the regression test after the lesson (d = 0.03).

The authors' reading: stating usefulness does little to make the lesson itself more engaging, so it does not make people learn more on the spot; what it affects is whether they want to come back to the topic later. The authors also point out that leaving an email address about 20 minutes after the lesson does not mean a student actually signed up for a statistics course.

The study set out to test one thing in particular: whether telling unconfident people "this is very useful" backfires. One of the seven experiments was designed and preregistered for this question, and it found nothing of the kind. In the pooled analysis, usefulness × confidence and × interest across seven outcomes made 14 tests, and only one was significant: the more confident people were, the more distraction they reported after being told about usefulness. The authors say these data had less than 30% power to detect interactions of this kind, so this means "not detected," not "shown to be absent."

Switching to knowledge material: Hecht and colleagues 2021, Study 1

Cameron Hecht and colleagues' two 2021 experiments changed the material: the biology of fungi, a task of remembering and understanding knowledge rather than practicing a skill. The usefulness information was built into the lesson video, and all of it was everyday examples (yeast in bread, mold at home, antibiotics); career examples were left out on purpose.

Study 1 had 185 college students. People who saw the usefulness version rated the content as more useful on average, but the main effect on task interest was zero. Interest did show a significant interaction: the more interested people were in fungi before learning, the more the usefulness information raised their interest. The authors did not report the effect at the high and low ends of interest separately, so there is no number behind "it does nothing at all for uninterested people." "Interested" is also relative here: the sample's starting interest in fungi averaged about 3 on a 7-point scale.

Study 1 did not measure learning. Also, the usefulness version of the video was longer than the control version; adding up the segment times given in the paper, I get about 12 minutes versus 8. The paper does not list this as a limitation.

The early mental-math experiments: Canning and Harackiewicz 2015

A frequently cited source for "stating usefulness hurts unconfident learners" is Elizabeth Canning and Judith Harackiewicz's three 2015 experiments. Participants learned a two-digit mental multiplication technique in the lab, in under an hour. The abstract says that directly communicated usefulness made performance and interest worse for people who lacked confidence.

After reading the whole paper, that sentence needs its comparison group. Study 1 had three groups: write about usefulness yourself, be told directly, and a control group told nothing. Unconfident people in the direct group scored slightly lower than the control group on performance and interest, but the differences were not significant. The significant comparison was a different one: unconfident people in the direct group performed worse than those in the "write it yourself" group. So the accurate statement is "for unconfident people, being told about usefulness did worse than writing about it themselves," not "being told about usefulness is worse than being told nothing." Study 2 did not reproduce the direct × confidence interaction. Study 3 compared two versions of the direct message; it is discussed under "Where the sources disagree" below.

The authors list one limitation themselves: the direct message came during learning, and the writing came after learning and practice, so the difference in results may come from timing rather than from the methods themselves.

All three experiments lasted only an hour, and the material was a skill that only pays off once mastered. Hecht and colleagues speculate (and Asher and colleagues repeat this in their introduction) that confidence matters so much here because a technique you can't execute is useless, whereas in a knowledge task, whatever you learn is usable. This is the authors' speculation; no study has manipulated task type within a single experiment.

Having readers write about usefulness themselves

The second move is having learners do the writing. Most of this research is in real classrooms, with graded assignments reviewed by teaching staff, which is far from one person reading an article. I order the studies by date because the results keep shifting.

High school science: Hulleman and Harackiewicz 2009

This is the original field experiment on usefulness writing, published in Science. I read the supplementary materials the publisher makes public, not the main text, so the numbers below come only from the supplement.

262 high school students were randomized individually within 19 science classes. The relevance group wrote a short essay before each exam, picking a current topic and writing how it related to their own lives or those of family and friends and to their future plans; the control group wrote a summary of the topic. Both groups' instructions came with an example about the digestive system, and the relevance group's example modeled a ready-made usefulness connection. Students wrote an average of 4.7 essays in the semester.

The result was an interaction: the lower students' expectation of success in their science class, the relatively higher their end-of-semester interest and second-quarter grades in the relevance group. For students with low expectations (one standard deviation below the mean), the model-predicted grades were 3.23 in the relevance group and 2.43 in the control group. Conditions:

• Grades came from only one school, 100 students, and the model did not control for earlier grades.
• The supplement reports only the interaction and predicted values; there is no test comparing the two groups among low-expectation students.
• The overall main effects were not significant and had a negative sign; for high-expectation students, both predicted values were slightly lower in the relevance group.
• 26% of the relevance group were rated as making no connection to their lives at all, and how well the connection was made had almost nothing to do with end-of-semester interest.

University biology: Harackiewicz and colleagues 2016

Judith Harackiewicz and colleagues' 2016 study ran for four semesters in an introductory biology course with 1,040 students, who wrote three assignments per semester. The usefulness group wrote about how course concepts related to their own (or others') lives; the control group wrote summaries. Assignments were graded and reviewed with feedback by graduate students.

For students overall, the effect of usefulness writing was very small (d = 0.06). The effect was concentrated among first-generation college students from underrepresented racial or ethnic groups: d = 0.55, and their grade gap with continuing-generation majority students narrowed by about 60%. This group had only 64 students across both conditions. First-generation students from the majority group did not benefit, as the authors state.

Unlike Hulleman 2009, students' confidence in their performance did not moderate the effect this time, which the authors mark as not replicated; what did moderate it was prior semester GPA, with larger effects the lower it was. This study measured interest only at the start of the semester, not at the end, so it cannot answer "does writing about usefulness raise interest."

Two-year colleges: Canning and colleagues 2019

Elizabeth Canning and colleagues' 2019 study took the method to introductory biology and psychology courses at two-year colleges in Wisconsin, analyzing 415 students. The difference from 2016: the assignment instructions in both usefulness groups came with the same examples of usefulness connections, offered in an instructor's voice in one group ("Here are some examples of an approach you could take") and framed as written by former students in the other. The control group wrote summaries.

The results went the opposite way from the previous two papers. Students with low first-exam grades (model predictions one standard deviation below the mean) reported lower end-of-semester interest and lower perceived usefulness of the course in the usefulness groups than in the control group. No difference was detected in course grades between the usefulness groups and the control group. Lower grades appeared only between the two usefulness groups: struggling students who got the "former students' examples" had lower grades than those who got the instructor's examples.

This study had no group that wrote about usefulness without examples, so it cannot tell whether the backfire came from writing about usefulness itself or from giving examples first and then asking students to write. The authors' own practical conclusion is aimed at the examples: until it is clear how to present them without threat, usefulness examples may put too much pressure on struggling students. The authors also say they cannot tell whether this is specific to two-year colleges or a matter of students' writing skills.

Remote upper-level courses: Shillington and colleagues 2025

Katie Shillington and colleagues' 2025 study ran in spring 2020, the first term in which courses moved online in an emergency because of the pandemic. Four junior- and senior-level biology courses with 1,243 students were assigned by discussion section to usefulness writing or summary writing, two essays each.

No difference was detected in course grades (d = 0.05). The usefulness group had slightly more page views and participation counts in the learning management system (d = 0.16 and 0.18). These two differences need discounting: assignment was by section but analysis was by student, with no correction for clustering, and both counts are cumulative over the whole term, including the time before the first essay. The study measured no interest, perceived usefulness, or any other psychological variable. The authors list online delivery, upper-level students, and the pandemic side by side as three possible reasons for the null result on grades, and the data cannot separate them. It was a credit course with instructors, discussion sections, and exams, so it is not evidence about self-study.

In the lab: hear it, then write it

Two lab studies tested the combination of "first hear about usefulness, then write about it."

• Canning and Harackiewicz 2015, Study 2: hearing about usefulness in the material and then writing about it was best for unconfident people on perceived usefulness, performance, and interest (all three three-way interactions significant).
• Hecht and colleagues 2021, Study 2: all participants watched the fungi video with usefulness information; afterwards, the group that wrote about usefulness answered about 1 more question correctly on average (out of 30) than the group that described two pictures. No difference was detected in post-test interest or in intentions to keep learning. The experiment had no group that saw no usefulness information at all.

Scaled up to MOOCs: Kizilcec and colleagues 2020

René Kizilcec and colleagues' 2020 study tested "value-relevance" writing, a neighbor of usefulness writing: in a survey at the start of a MOOC, learners ticked two or three values they cared about and wrote how taking the course reflected them. The study put this kind of writing into 247 courses and more than 260,000 learners; I cite only the part relevant here.

The activity had earlier raised completion rates sharply for students from developing countries in two courses. At scale, it helped students from less developed countries only in courses that already had a completion gap between countries in the control group, by about 2.8 percentage points, replicated in both years; in courses without such a gap, the same group's completion rate went down instead. Which courses counted as "having a gap" was defined after the fact in the first year, and the authors warn this may have produced the pattern. The authors also say the results should not be extended to less engaged students or other educational settings.

Giving readers a choice

For letting readers pick their own example or framing, I found direct evidence in only one study: Asher and Harackiewicz's, above. Of its seven experiments, the third through the seventh included a choice manipulation. The choice group picked one of three regression videos before the lesson; the three were framed with different datasets and research questions, but the content and sequence were identical. In the control group, each person was paired with someone in the choice group and assigned whichever video that person picked.

• Perceived autonomy was clearly higher in the choice group (d = 0.92).
• In-the-moment interest was higher (d = 0.24), reported distraction was lower, and maintained interest in regression was also higher (d = 0.16).
• No difference was detected on the regression test after the lesson, nor in requests for statistics resources.
• One experiment offered only two videos, one of which most people in a pilot did not want to watch; no difference from the standard choice group was detected in autonomy or either kind of interest. The authors infer that having a choice at all matters more than getting content that matches one's taste.

In this study no interaction between the two moves was detected. The authors think the two work through separate mechanisms and their effects can add up; but the interaction was tested only in the third and fourth experiments, and the authors first say this may simply reflect low power.

Asher and colleagues use Hidi and Renninger's model of interest to explain the choice group's results; I did not find a legally available full text of that model. I did not obtain the full text of any meta-analysis of choice and motivation. So this section rests on one study, one kind of choice (picking a framing), and single sessions.

Interesting details unrelated to the main point

The dissertation version of the meta-analysis: Sundararajan 2018

Chapter 2 of NarayanKripa Sundararajan's 2018 dissertation is a meta-analysis that was later rewritten as Sundararajan and Adesope's 2020 journal article. I did not find a legally available full text of the journal version, so the numbers below can only be cited as the dissertation version; the journal version's study counts and effect sizes may differ.

Across 54 comparisons and 5,111 participants, groups whose material included irrelevant details scored 0.43 standard deviations lower on immediate tests (g = −0.43). This number has to be read alongside the author's own caveats:

• Both publication-bias tests were significant. Of the 11 studies with the largest effects, 6 shared one co-author; without those 6, the overall effect became −0.28. The author's conclusion is that the direction is confirmed but the size cannot be pinned down.
• The 17 comparisons rated high in quality came to −0.24.
• 50 of the 54 comparisons were in the lab; only 4 were in classrooms, where no difference was detected.
• Only 2 studies measured delayed effects, so the conclusion is limited to immediate tests.
• 26 of the 54 studies did not report how they confirmed that the details were really interesting and really irrelevant.

The author wanted to test many moderators, and few between-group differences were significant. Only one bears on writing: details presented in two media at once (text plus an image, for example) did more harm than details in one medium. This is a between-study grouping, which the author calls correlational evidence. Another one, the format of the details (text plus image worst), is printed as significant in the table, but the statistic in the table does not correspond to that p value, so I do not treat it as a result. For the other features relevant to writers, no between-group difference was detected: placing details at the start, in the middle, or at the end; how much of the page they take up; what share of the material they make up; staying on screen or appearing intermittently; whether learning objectives were given first. The planned analysis of prior knowledge was not done, because only about a quarter of the studies reported objective prior-knowledge scores.

Chapter 3 of the dissertation adds an experiment: college students watched narrated slides on the gas laws, with four groups whose share of slides carrying irrelevant images ranged from none to all. Average post-test scores dropped slightly as the share went up, but the effect of the share was not significant. The experiment has two weaknesses: pretest scores were almost all zero, and after randomization the control group had a clearly higher share of students who had taken a related chemistry course (74%, versus about 40 to 50% in the other three groups), which would push the control group's post-test scores up.

Chapters 4 and 5 are an infographic and a blog draft meant for outreach. They say "If you really want to include seductive details, share it quickly, at the beginning, using just one medium" and "Novice learners are more susceptible". The "beginning" in the first statement rests on a single study in the meta-analysis with a nonsignificant between-group test; the second statement could not be tested with the dissertation's data. Neither is a research result.

How much: Wesenberg and colleagues 2026

Lukas Wesenberg and colleagues' two 2026 experiments changed one thing only: what share of the material the irrelevant text took up. The insertion points were fixed at three, and what changed was how long each insertion was, so this is the effect of "how long at each point," not "at how many points." The irrelevant text sat directly inside the main text, with no box and no label. The materials were German expository texts of 600 words (solar cells) and 960 words (the carbon cycle).

In both experiments, the higher the share of irrelevant text, the worse the recall. Going from 0% to 50%, recall in the second experiment was about 16.5 percentage points lower when converted from the regression coefficient (my conversion; the paper does not give group averages). The first experiment's effect was smaller: the simple correlation between recall and share was not significant and became significant only after controlling for working memory and prior knowledge. No difference was detected on transfer questions in either experiment.

These fun facts did not buy any motivation either: no change with the share was detected in intrinsic motivation or self-reported cognitive load. No moderation by prior knowledge was detected, but the authors say this may be a floor effect: average prior knowledge in both samples was under a tenth of the maximum score, so almost nobody knew the material.

The authors' practical advice is that small amounts probably do no noticeable harm and large amounts should be avoided. The data themselves show no "small amounts are harmless" threshold; recall declines in a straight line. In the second experiment, a curve model added after the fact for transfer suggested small amounts might help, and the authors themselves say that model is unstable.

Mandatory or voluntary: Wesenberg and colleagues 2025

The same team's two 2025 experiments asked whether being required to learn, versus wanting to, changes the effect of fun details. Participants were German-speaking college students recruited online. Each studied two units of about 700 words each; the instruction page said that completing one unit was mandatory and required for the participation payment, and that the other was only voluntary, with no payment for it; the voluntary one could really be skipped by clicking through five pages. Half the participants saw irrelevant text and images in both units.

• Mandatory units: the group with irrelevant details scored lower, in both experiments.
• Voluntary units: in the first experiment the group with irrelevant details scored higher, p = .048; in the second experiment (irrelevant details cut from five to two), no difference was detected.
• Voluntary units produced little learning overall: scores were less than half those in the mandatory units, and time spent was about two minutes versus more than four.
• The irrelevant details raised self-reported interest in the first experiment, with no difference detected in the second; no increase in reading time was detected in either experiment.

The authors draw their conclusion narrowly: it holds only for people who subjectively experienced the units as mandatory or voluntary (in each experiment, roughly 16 to 17% of participants rated the external pressure in the voluntary unit as no lower than in the mandatory one and were excluded), and they say explicitly that they cannot yet recommend adding such content in voluntary settings. "Voluntary" here is one section of a paid experiment labeled voluntary, not an article a reader went looking for.

What these studies did not measure

"An interesting story keeps readers reading" is the most common reason for adding fun facts. Participants in these experiments could not leave to read something else, so continued reading was never measured. The closest thing is the reading time in Wesenberg 2025: the versions with irrelevant details had more words, yet reading time was not significantly longer. As for "putting fun facts in a box or at the end makes them harmless," the introduction of Wesenberg 2026 reports that some studies claim this; I have not read those studies. In the dissertation version of the meta-analysis, only 3 studies placed details at the end, and no difference from other positions was detected.

The interest readers already have

Everything above manipulates something the author controls. Whether readers are already interested in a topic is a different matter. Virginia Clinton and Paul van den Broek's two 2012 studies had college students read two science articles adapted from Scientific American, rating their interest in each topic beforehand.

The more interest people reported before reading, the more they recalled afterwards, in both studies and for both articles; on the comprehension test, this held in three of four checks. In the second study, participants had to say what they were thinking after every sentence, and interested readers made more inferences for one article but not the other. Afterwards, the authors ran a text-analysis tool and found that article to be more coherent, and they speculate that interest drives inferences only in coherent texts; the two articles also differed in topic, difficulty, and readers' average interest, and this explanation was not tested.

Both studies are correlational: interest was not manipulated, so they cannot be read as "make readers interested and they will remember more." The authors themselves rate the role of inferences as "relatively small."

Who it works for: the moderators side by side

The question of this post is "who does each move work for." Here are the reader differences the studies tested, in one table:

Two things stand out. First, the same reader characteristic often gives different results in different studies. Take "does writing about usefulness help unconfident people more": only Hulleman 2009 had a significant interaction; Canning 2015 Study 1 and Hecht Study 2 had only a simple effect at the low-confidence end, the former reporting no interaction test, the latter with a nonsignificant interaction and a hear-then-write design; Canning 2015 Study 2 and Harackiewicz 2016 both did not detect the interaction. Splitting by prior grades instead, Harackiewicz 2016 (the lower the prior GPA, the larger the effect on grades) and Canning 2019 (people with low first-exam grades reported lower interest and perceived usefulness) point in opposite directions, but they measured different outcomes: Canning 2019 did not detect this interaction on grades. Second, there are almost no testable data on "who is hurt more by irrelevant details"; these sources cannot support claims like "novices are more easily distracted by fun facts."

Where the sources disagree

The results below point in different directions, or seem to conflict while actually comparing different things. I list them side by side without picking a side.

Does stating usefulness hurt unconfident people? The abstract of Canning and Harackiewicz 2015 says it does, but the comparison behind that sentence is "writing about usefulness yourself"; against a control group told nothing, none of the three experiments detected significant harm. The table in their Study 3 shows that the two direct versions combined had a positive main effect on interest against control, not moderated by confidence (the text attributes this effect to a different contrast, so the table and text disagree). Asher and colleagues' experiment designed for this question found nothing either. When Hecht and colleagues used a different model in Study 1, the confidence interaction turned significant and in the opposite direction (the more confident, the less the usefulness information helped interest); it disappeared once the part shared with interest was removed, and the text does not discuss it. The studies at the root of this line, Durik and colleagues 2007 and 2015, I did not read in full; Hecht and colleagues report that the 2015 paper concluded it was confidence, not interest, doing the moderating.

Are everyday examples better than career examples? Canning and Harackiewicz 2015, Study 3, compared two direct versions: everyday examples only, and everyday plus career examples. For unconfident people, the everyday-only version produced higher interest; perceived usefulness fell just short of significance, and no difference was detected in performance. For confident people, the version with career examples did better by raising confidence. Hecht and colleagues used only everyday examples in their usefulness video on this basis, as a design choice, without comparing against career examples. Asher and colleagues used exactly career uses, and across seven experiments detected no harm to unconfident people.

Does writing about usefulness help or hurt lower-achieving students? In Hulleman 2009, high schoolers with low expectations of success benefited; in Harackiewicz 2016, college students with low prior GPA benefited, but confidence did not moderate; in Canning 2019, two-year college students with low first-exam grades reported lower interest. The assignments differed: in 2019 both usefulness groups got examples; in 2009 both the control and relevance groups' instructions came with an example; the 2016 methods section mentions no examples, and the 2019 paper says 2016 gave only brief hypothetical ones. The three also measured "achievement level" differently (self-reported expectations, prior GPA, first exam).

Do more irrelevant details hurt more? Both Wesenberg 2026 experiments found that more meant worse recall. In Sundararajan's meta-analysis, the proportion groups show no dose relationship (studies where details made up 1 to 25% and studies where they made up 100% had the same effect size), and the share was not significant in the dissertation's own experiment either. Wesenberg and colleagues' explanation is that in studies that found no harm, the details were decorative pictures or were placed in boxes; that is their speculation. The two also measure "amount" differently: Wesenberg fixed the insertion points and varied length; the meta-analysis coded proportion across studies.

Staying on screen or appearing briefly. The post on diagrams cited the journal version's grouping secondhand through another meta-review: details that stay on screen did more harm. In the dissertation version, no between-group difference was detected between continuous and intermittent details. These are two versions of the same analysis; I have not read the journal version and cannot tell where the difference comes from.

Do irrelevant details make readers more interested? Yes in the first Wesenberg 2025 experiment, no difference detected in the second; in Wesenberg 2026, no increase in intrinsic motivation with the share was detected; in Sundararajan's experiment, slides with details were rated more interesting, but on the same slide students more often picked the content image as the most interesting part, and most said the images did not help them learn.

Abstracts that say more than the results. Shillington and colleagues' abstract says the intervention "had a positive effect" and their conclusion says it was "successful," based on page views and participation counts; the primary outcome they set themselves was grades, where no difference was detected. Asher and colleagues' abstract says "only the utility value manipulation led students to request resources about statistics," but the difference between direct usefulness and choice was not significant. Hecht and colleagues' abstract says future-oriented usefulness writing "further promoted interest development," but the interaction on the outcome that directly measured interest was not significant; what was significant was self-reported intentions and perceived usefulness.

What you can do

These are this site's judgments, each with its basis; "basis" names the results that led me here, not a study that tested the practice directly.

1. When you state usefulness, say concretely where it's used, and don't expect it to make readers learn more. For example (my own), instead of "gradient descent is extremely important," write "when you call model.fit() in Keras, this is the loop that runs; the learning rate you set in the optimizer is how far each step goes." Basis: in Asher's seven experiments and Hecht's Study 1, stating usefulness made people rate the content as more useful, with no difference detected in immediate test scores. A usefulness sentence changes whether readers think the material is worth it, not how much they learn.
2. Pick usefulness examples readers can run into now, before talking about careers. The basis is weak: only Canning 2015 Study 3 saw this, on one outcome, and the direction reversed for confident people; Hecht and colleagues designed around this principle without comparing. This is mainly this site's choice, on the grounds that the problems on readers' desks are more concrete than future jobs.
3. Don't ask readers to write a passage on "what this does for me"; if you include it, make it a one-line prompt they can skip. Basis: all the evidence on writing about usefulness comes from graded, reviewed course assignments, and the results flip across students and courses; the version with examples backfired for struggling students at two-year colleges; scaled up to MOOCs, the neighboring value writing had a small effect in some courses and lowered completion in others. Whether readers do the activities in an article was covered in an earlier post.
4. Don't rewrite an article just to "give readers a choice." Basis: there is only one direct study, the choice was a framing, and no difference was detected in test scores. If you already have two examples with different framings that teach the same thing, you can include both and let readers pick which to read first; that is this site's choice, and no study has tested it in an article.
5. Leave out fun facts unrelated to the argument; if you must include one, keep it short, keep them few, use one form only, and don't pair text with an image. Basis: the meta-analysis points to harm, size uncertain; in Wesenberg 2026, longer meant worse recall; the greater harm from two media is a between-study grouping. There is no evidence on where they do less harm, so don't tell yourself "it's fine at the start."
6. An opening "scene" should be a question the main text answers. Basis: by definition, a story directly tied to the question the main text answers is not an irrelevant detail; but none of these sources compared "a relevant opening" with "no opening," so this is this site's choice. A check: if you delete the opening, does any later section need to refer back to it? If not, it's a fun fact.

Checked against this site's writing specs

Two specs on this site bear on this topic (series-curriculum-design and course-guide-contract.md), plus one practice in existing guides, as of the working directory on 2026-10-14 (spec wording translated from Chinese):

As of 2026-10-14, the specs have not changed because of this post. Changing a skill goes through the .agents/skills/ process; this table only lists suggestions.

Three things to do tonight

Pick a teaching article you've written; about half an hour:

1. Mark every story, fun fact, and historical aside. For each one, ask: if I delete this, can readers still answer the question this article answers? If yes, and the passage isn't stating usefulness, delete it or cut it to one sentence.
2. Search for words like "important," "very useful," and "must-learn." Replace each with one concrete use: in what situation, doing what, readers will use it.
3. Look at the first paragraph. If it's a question, make sure the article actually answers it later; if it's a fun fact loosely tied to the topic, turn it into the question readers will be able to answer after reading.

Limits of this evidence

• No study directly tested one person reading a web article. The direct-usefulness experiments had college students watch videos in a lab; the write-it-yourself studies are graded course assignments; most irrelevant-detail studies are in labs with short materials: the two newer sets of experiments used 600 to 960 words, and fewer than half the studies in the meta-analysis reported study time, few of them over 15 minutes. Carrying any of this to web guides is my inference.
• Nearly all the usefulness research comes from one group. Apart from Shillington and colleagues and Kizilcec and colleagues, all six other papers have Harackiewicz as an author. The two newer sets of experiments on irrelevant details come from one German team, with the same materials and raters.
• Almost all tests were immediate. Interest in the usefulness studies is mostly self-report filled in right after learning; Asher's furthest "follow-up behavior" is leaving an email about 20 minutes after the lesson; only 2 studies in the irrelevant-details meta-analysis measured delayed effects.
• Low power. Asher and colleagues put power to detect interactions below 30%; in these studies, "no moderation detected" can mostly only be read as "not detected." The studies ran many tests, mostly uncorrected.
• Versions. For Hulleman 2009 I read only the publisher's public supplementary materials; for Sundararajan, the dissertation, not the journal version; for Asher, Canning 2015, Harackiewicz 2016, and Hecht 2021, author manuscripts on PMC; for Clinton 2012, the pre-publication proof.
• Inconsistencies inside the sources. Asher and colleagues' text describes the only significant moderation as an interaction with "baseline interest in statistics," while the table and the authors' public data list it under confidence; in Canning 2015 Study 3, the table and the text attribute one main effect to different contrasts; the tables in Sundararajan's dissertation have several errors (statistics that don't match p values, misaligned confidence intervals, a study count given as both 54 and 72). Throughout, I follow the tables and note the issues in the appendix.
• My inferences and judgments: carrying the results to web guides; "the scene should be a question the main text answers"; the "would a later section refer back to the opening" check; choosing usefulness examples readers can run into now; the six items under what you can do; the verdicts in the spec table. All are marked in the text.
• Numbers I computed: the lengths of the two videos in Hecht Study 1 (from the segment times in the paper); the 0% to 50% recall difference in Wesenberg 2026 (from the regression coefficient). A few more in the appendix, each marked.
• Secondhand citations: Durik and colleagues 2007 and 2015 (as reported by Hecht and colleagues), Wang and Lewis 2022 on an online inorganic chemistry course (cited by Shillington and colleagues, also no difference in grades), and the "put it in a box" studies reported in Wesenberg 2026's introduction; I have not read any of the originals.
• Known to exist, but no legally available full text found: Hidi and Renninger (2006)'s four-phase model of interest, Sundararajan and Adesope (2020)'s journal meta-analysis, Cheng and colleagues' newer meta-analysis of irrelevant details (online 2025), Durik and Harackiewicz (2007), and Durik and colleagues (2015). None of their numbers are cited and none are in the references. Rey's earlier 2012 meta-analysis, Brock and colleagues' 2025 study of physics videos, and the full version of Hulleman and colleagues 2010 I either did not obtain or did not finish.
• Files on hand but not in this round of close reading: Priniski and colleagues 2019 (writing about usefulness for yourself plus for others), Lazowski's 2015 dissertation (a meta-analysis of motivation interventions), and Wang and colleagues 2024 (a meta-analysis of self-determination-theory interventions).

Appendix: design and numbers for each study

The main text keeps one or two numbers per item; the rest are here.

Asher and Harackiewicz (2025), Journal of Educational Psychology 117(4), online 2024-11-11. Read the PMC author manuscript and the pooled-results file in the authors' OSF project; supplementary materials not obtained. Seven experiments, spring 2020 to fall 2022, introductory psychology students at the University of Wisconsin–Madison, 2,019 in total; about 59% women, 74.2% white, 84% first-year. Experiments ranged from 100 to 673 people; two were run over video. Only the second and fourth experiments and the pooling procedure were preregistered. Procedure: baseline survey (math confidence, interest in statistics) → manipulation → regression lesson video → survey → resource request → 12-minute timed test. Pooled main effects (control = without that manipulation): direct usefulness on perceived usefulness d = 0.41 (p < .001), autonomy 0.12 (p = .079), triggered interest 0.08 (p = .094), distraction 0.01, maintained interest 0.15 (p < .001), log odds of requesting resources 0.30 (OR = 1.35, p = .042; 39.2% vs 33.2%), test score 0.03 (p = .463). Choice: perceived usefulness 0.09 (not significant), autonomy 0.92, triggered interest 0.24, distraction −0.15 (p = .017), maintained interest 0.16, resource requests OR = 1.02 (p = .885), test score 0.04 (p = .458). Differences between the two manipulations: triggered interest p = .043; distraction p = .055; resource requests p = .134. Moderation: of 14 tests of direct usefulness × interest and × confidence, only distraction × confidence was significant (0.17, p = .006); the text describes it as an interaction with interest in statistics, while the table and OSF file say confidence; maintained interest × interest −0.08 (p = .082), negative in direction. Interactions between the two manipulations (third and fourth experiments, 773 people) were all nonsignificant, ps ≥ .382. For resource requests, only the fourth experiment showed a significant direct-usefulness effect on its own (OSF file). Limitations listed by the authors: emerging individual interest measured with one binary indicator, interest entirely self-reported, no measure of prior knowledge, college students from one school; power below 30%.

Hecht, Grande, and Harackiewicz (2021), Motivation Science 7(1), online 2020-04-30. Read the PMC author manuscript, with tables checked against the HTML structure. Study 1: 185 people (control 61, usefulness 124), a lesson video on fungi, usefulness information all everyday examples. Residualized-interest model: usefulness on task interest β = .01 (p = .877); × initial interest β = .16 (p = .010); on perceived usefulness β = .15 (p = .017), × initial interest β = .21 (p = .001); main effect and interaction on task confidence both nonsignificant. Residualized-confidence model: interactions all nonsignificant (task interest β = −.06, p = .418); in the dual-moderator model, usefulness × confidence on task interest β = −.13 (p = .048). No simple effects reported at high and low interest. Initial interest averaged 3.11 (7-point scale). Study 2: 408 people; all four groups watched the usefulness video, then wrote for 10 minutes (standard usefulness, future usefulness, present usefulness, describe pictures). Test (30 questions): the three usefulness-writing groups combined 21.94 (SD 4.74) vs control 20.90 (5.16), β = .12 (p = .012); a rough conversion using the full-sample standard deviation gives about 0.21 standard deviations, computed during extraction, not a number from the paper. × task confidence β = −.07 (p = .111; the text prints it as positive); simple effects: low confidence β = .17 (p = .007), high confidence β = .03 (p = .658). Post-test interest β = .05 (p = .141) and behavioral intentions β = .05 (p = .223), not significant. Future vs present main effects nonsignificant on all six outcomes; future × task interest on behavioral intentions β = .11 (p = .012), on post-test interest β = .06 (p = .059). The future and present prompts included examples and the standard one did not, a confound the authors point out themselves. Limitations listed by the authors: few participants from minority groups, confidence measured differently before and after, a single one-hour lab session.

Canning and Harackiewicz (2015), Motivation Science 1(1). Read the PMC author manuscript; figures and appendices not obtained, and cell-level predicted values appear only in the figures. All three experiments taught two-digit mental multiplication in under an hour. Study 1, 88 people: writing it yourself vs direct, performance M = 30.36 vs 26.48 (p = .040), × confidence p = .035; the same interaction for interest p = .065. Against control (d): direct, low-confidence perceived usefulness −.13, performance −.18 (p = .41), interest −.20 (p > .20); high-confidence perceived usefulness .70 (p < .01). Writing it yourself, low-confidence performance .59 (p = .01). Study 2, 113 people, 2 × 2: main effects of direct and direct × confidence all nonsignificant; direct × writing × confidence, perceived usefulness p = .027, performance p = .018, interest p = .015. Study 3, 134 people: comparing the everyday-only version with the standard version (everyday plus career), × confidence on interest β = −.16 (p = .010), on perceived usefulness p = .055, no effect of any kind on performance; in the table, the two direct versions combined against control give perceived usefulness β = .26 (p < .001) and interest β = .14 (p = .028), neither moderated by confidence. In Studies 1 and 2, confidence was measured after learning the technique. Over 90% of participants were white. Limitations listed by the authors: one paradigm, lab, one hour; timing confound; weaker replication than the original studies.

Hulleman and Harackiewicz (2009), Science 326. Read only the publisher's public supplementary materials, not the main text. 262 high school students (two schools, 7 teachers, 19 classes), randomized individually within classes: relevance 136, control 126. Students wrote 1 to 8 essays in the semester (M = 4.7). Manipulation check: connections to life in the essays 0.91 vs 0.10 (0–2 scale). End-of-semester interest in science: group main effect β = −.08 (p = .15); group × expectation of success β = −.11 (p = .05); predicted values, low expectation relevance 3.91 vs control 3.55, high expectation 3.67 vs 3.76. Second-quarter grades (one school, 100 people): main effect β = −.03 (p = .69); interaction β = −.19 (table), given as −.18 in the supplement's text (p = .03); predicted values, low expectation 3.23 vs 2.43, high expectation 2.81 vs 3.03. No significant effect on intentions for future courses and careers. 26% of the relevance group made no connection; connection strength vs end-of-semester interest, none vs moderate d = .00, none vs strong d = .11. The grade model did not include earlier grades.

Harackiewicz, Canning, Tibbetts, Priniski, and Hyde (2016), JPSP 111(5), online 2015. Read the PMC author manuscript. Four semesters, 1,040 people, a 2 × 2 of usefulness writing × values affirmation; values affirmation had no effect of any kind and was collapsed. Course grades: usefulness main effect β = 0.08 (p = .024), 2.81 vs 2.76, d = 0.06; × underrepresented group p = .092 (the interaction underlying the authors' 40% reduction in the racial achievement gap did not reach significance); × first-generation p = .808; three-way interaction β = 0.08 (p = .015). First-generation students from underrepresented groups, 64 people: treatment effect .51 grade points (d = 0.55), gap reduced by 61%. × confidence in performance p = .203; × prior GPA β = −0.05 (p = .045). Word count partially mediated the three-way interaction. In an exploratory model excluding first-generation underrepresented students, the usefulness main effect was β = −0.01 (p = .813). No end-of-semester measure of interest or perceived usefulness. Limitations listed by the authors: small numbers per racial/ethnic group, first-generation status as a binary indicator, the explanation that these students' goals clash with the culture of science is speculative.

Canning, Priniski, and Harackiewicz (2019), Learning and Instruction 62. Read the published version made public by ERIC. Introductory biology and psychology taught by 11 instructors at 6 campuses of a Wisconsin two-year college system; 521 enrolled, 415 analyzed. Three 500-word essays per semester, worth 1% to 4% of the course grade. Usefulness vs control: interest main effect β = −.04 (p = .349), × first exam β = 0.14 (p = .003), struggling students β = −0.18 (p = .007; predicted 4.65 vs 5.01); perceived usefulness, struggling students β = −0.14 (p = .037); course grade main effect β = −.05 (p = .135), interaction p = .829. Student-framed vs instructor-framed: struggling students' grades β = −0.11 (p = .032); high performers' interest β = 0.15 (p = .031). Interest and perceived usefulness measured only in week 13, with no baseline. In 7 of 11 courses, the first essay was assigned before the first exam. Several errors in the tables (the p column of one word-count row matches the β column of the personal-pronouns row; some predicted values for process variables fall below the scale minimum).

Shillington, Lo, and Hobbie (2025), Frontiers in Education 10. Read the published version and the supplementary materials. Spring 2020, four upper-level biology courses at UC San Diego, five instructors; 1,243 people (usefulness 589, control 654), cluster-assigned by discussion section and analyzed by student, with no clustering correction and no reported number of sections. Two essays. Grades 88.98 vs 88.60 (out of 100), d = 0.05 (p = .39). Page views 858 vs 798 (d = 0.16, p = .006); participation counts 40.49 vs 38.86 (d = 0.18, p = .002). Underrepresented group × condition F = 0.057 (p = .81). The usefulness group wrote longer essays with more personal pronouns; the prompt itself asked for two extra paragraphs on personal and other-oriented applications and allowed personal pronouns. For social-process words, the t and d printed in the paper do not match the mean difference.

Kizilcec, Reich, Yeomans, and colleagues (2020), PNAS 117(26). Read the published version and the SI. 247 MOOCs from Harvard, MIT, and Stanford, September 2016 to May 2019, focal sample 269,169, intent-to-treat analysis. Value-relevance writing: in two earlier courses it raised completion for students from developing countries from 17% to 41%; the earlier effect the authors compare against is 24 percentage points, from a sample of 64. At scale, across all courses combined, no difference was detected for students from less developed countries; in courses with a global gap, +2.79 percentage points (year 1) and +2.74 (year 2); in courses without a gap, −1.62 and −1.71. The authors call this an order of magnitude smaller than before. The global gap was defined after the fact in year 1. A full treatment of this study will come in the later post on why readers don't finish.

Sundararajan (2018), Washington State University dissertation, institutional repository version. Meta-analysis: searched through September 2018, 54 effect sizes, 5,111 people (the narrative also says 72; all the tables sum to 54); a single coder, no agreement statistic. Random effects g = −0.43 (−0.55 to −0.31), I² = 72.82. Recall only −0.46 (k = 15), transfer only −0.18 (k = 4, not significant), both combined −0.45 (k = 35). Egger and Begg tests p < .01; without the 6 studies sharing one co-author, −0.28. Quality: low −0.52, medium −0.53, high −0.24 (between-group p = .08). Setting: lab −0.46 (k = 50), classroom −0.15 (k = 4, not significant). Media: one −0.35 (k = 37), two −0.73 (k = 14), between-group p = .01. Format (text plus image −0.94, k = 10): the between-group statistic and p value don't match (QB = 9.40 with df = 5 corresponds to p of about .09, computed during extraction with the chi-square distribution, not a number from the paper; the table prints .01). Position: start k = 1, interspersed −0.43, end −0.55 (k = 3), between-group p = .81. Proportion: 1–25% −0.61, 26–50% −0.42, 100% −0.61, between-group p = .56. Continuous −0.49, intermittent −0.36, p = .28. Learning objectives given −0.27, not given −0.56, p = .06. Majoring in or having taken the subject −0.26 (not significant), not −0.54, p = .15. Only 2 studies with delayed effects. Experiment: 169 people, 14 slides, about 12 minutes of narration; post-test for the 0%/25%/50%/100% groups 5.75, 5.48, 5.28, 5.01 (out of 10); effect of proportion p = .13, p = .406 after adding course experience; pretest averages below 1 point in all four groups; taken a related chemistry course 74% vs 43% to 51% (p = .013). In the three groups with details, 65%, 58%, and 75% said the detail images did not help.

Wesenberg, Jansen, Krieglstein, Meusel, Schneider, Valtin, and Rey (2026), Instructional Science 54. Read the publisher's open-access page and table pages; figures not seen, and the paper reports no group means. Study 1, 191 people (Prolific), 600 words, 0%/25%/50%; Study 2, 101 people (university recruitment), 960 words, 0% to 50% in 12.5% steps. Recall: b = −0.11 (p = .030) and −0.33 (p = .005), in units of change in recall score (percent of maximum) per one-percentage-point increase in share; no curve model beat the linear one. Transfer: b = −0.07 (p = .367) and −0.17 (p = .169); Study 2's post hoc cubic model p = .034, unstable under cross-validation. No difference detected in extraneous cognitive load or intrinsic motivation. × prior knowledge and × working memory all nonsignificant; average prior knowledge 9.54% and 7.67% of the maximum. Study 1's group sizes sum to 182, which does not match N = 191. Study 1's transfer test reliability .42.

Wesenberg, Jansen, Krieglstein, Schneider, and Rey (2025), Learning and Instruction 96, online 2024-11-26. Read the published version in the University of Zurich repository (CC BY). Study 1 recruited 150 and analyzed 120; Study 2 recruited 270 and analyzed 210; about 16% to 17% in each were excluded for rating the external pressure in the voluntary unit as equal to or higher than in the mandatory unit. Carbon cycle 727 words, nitrogen cycle 699 words. Study 1 had one irrelevant detail per page (about 30% of the main text), Study 2 two in total (about 12%). Test out of 24, adjusted means: Study 1 mandatory 11.56 (without) vs 9.55 (with), p = .041; voluntary 4.34 vs 6.15, p = .048; Study 2 mandatory 10.55 vs 9.04, p = .032; voluntary 4.04 vs 4.98, p = .128. Both interactions p = .002. In voluntary units, unadjusted standard deviations exceeded the means. Time spent: Study 1 about 276 seconds mandatory vs about 116 voluntary; Study 2 about 255 vs 114; main effects of irrelevant details all nonsignificant. Interest (8–56): Study 1 with details 43.64 vs 36.84 (p < .001); Study 2 p = .066. No difference detected in cognitive load (single item). Standardized differences computed during extraction from the appendix's unadjusted means and SDs: Study 1 mandatory −0.44, voluntary +0.20; Study 2 mandatory −0.35, voluntary +0.17 (not numbers from the paper).

Clinton and van den Broek (2012), Learning and Individual Differences 22(6). Read the publisher's proof made public by ERIC. Study 1, 60 people reading silently; Study 2, 69 people thinking aloud; two articles adapted from Scientific American, 32 sentences each, read one sentence at a time on screen. Interest and recall r = .30 to .49; controlling for the pretest, interest predicted recall β = .28 to .47. Interest predicting post-test: significant for both articles in Study 1; in Study 2, moon article β = .41, songbirds article β = .15 (p = .20). Interest and number of inferences: moon r = .38, songbirds r = .16 (not significant); inferences partially mediated the link between interest and post-test, but not between interest and recall. Study 2's pretest internal consistency was −.04 and .03, with pretest scores near zero. Thinking aloud raised songbirds post-test scores over silent reading (d = .69).

References

Each was read through in the version I could obtain, with an extraction record; what I could not read is noted in parentheses.

• Asher & Harackiewicz (2025), Using Choice and Utility Value to Promote Interest (PMC author manuscript; DOI 10.1037/edu0000921; pooled results also checked against the authors' OSF project; supplementary materials not obtained).
• Hecht, Grande & Harackiewicz (2021), The Role of Utility Value in Promoting Interest Development (PMC author manuscript; DOI 10.1037/mot0000182; only figure captions read).
• Canning & Harackiewicz (2015), Teach It, Don't Preach It (PMC author manuscript; DOI 10.1037/mot0000015; figures and appendices not obtained).
• Supplementary materials for Hulleman & Harackiewicz (2009), Promoting Interest and Performance in High School Science Classes (read only the publisher's public Supporting Online Material; main text not read; DOI 10.1126/science.1177067).
• Harackiewicz, Canning, Tibbetts, Priniski & Hyde (2016), Closing Achievement Gaps with a Utility-Value Intervention (PMC author manuscript; DOI 10.1037/pspp0000075).
• Canning, Priniski & Harackiewicz (2019), Unintended consequences of framing a utility-value intervention in two-year colleges (published version made public by ERIC; DOI 10.1016/j.learninstruc.2019.05.001; online supplementary materials not obtained).
• Shillington, Lo & Hobbie (2025), A utility value intervention to support student engagement in online upper-level undergraduate courses (published version and supplementary materials).
• Kizilcec, Reich, Yeomans et al. (2020), Scaling up behavioral science interventions in online education (published version on PMC and SI Appendix).
• Sundararajan (2018), Seductive details: A meta-regression and empirical study (Washington State University dissertation, institutional repository version; the journal version, Sundararajan & Adesope 2020, not read).
• Wesenberg, Jansen, Krieglstein, Meusel, Schneider, Valtin & Rey (2026), The more, the worse? The influence of the seductive detail amount on learning (publisher's open-access page and table pages; figures not seen).
• Wesenberg, Jansen, Krieglstein, Schneider & Rey (2025), The influence of seductive details in learning environments with low and high extrinsic motivation (published version in the University of Zurich repository, CC BY).
• Clinton & van den Broek (2012), Interest, inferences, and learning from texts (publisher's proof made public by ERIC; DOI 10.1016/j.lindif.2012.07.004).
• Posts on this site: Examples and openings in teaching articles, Questions and wording in teaching articles, When a teaching article needs a diagram, What the evidence for learning by doing measures, MIT 6.7960 Lecture 8 guide.