Writing the Examples and Openings of a Teaching Article: Evidence on Worked Examples, Explanations, Learning Objectives, and Reader Level

🌏 中文版

This is part 1 of the series "Writing Articles That Teach." It covers the first half of the text itself: how to write examples and explanations, and how to arrange the opening and structure of an article. The second half (questions inside the article, feedback, wording, and a clause-by-clause check of this site's writing spec) is in a companion article. Diagrams are in the article on visuals; video is in where to put the video and how video and text share the screen.

The trigger was this site's course guides. They follow a writing spec that requires the author to define, before writing, what the reader will be able to do afterward. The body must contain one example worked all the way through and self-checks with an answer or a criterion, and prerequisites the series has not taught need links. The spec ends with a list of design rationale, most of it with no indication of how strong the evidence is. These two articles go back and check: what experiments has educational psychology run on how to write explanatory text, how large were the effects, and how far do the authors themselves think the conclusions reach.

The site already has an article written from the learner's side. Learning How to Learn covers techniques readers can apply on their own. This one switches to the writer's side: given the same findings, what can an author do inside the article on the reader's behalf.

First, how these studies were chosen and read, because it changes how to read everything below. The scope is the effect on learning outcomes of things an author can manipulate inside an explanatory text, with meta-analyses first (studies that pool the results of many experiments into one estimate). My first pass started from researchers and topics I already knew, searching and selecting at the same time. Only afterward did I run a systematic scan and check for topics I had missed. The studies that made it in lean clearly one way: English-language literature, college-student participants, mathematics and natural science content, and studies whose full text I could obtain. Self-learners reading long web articles, and Chinese and Japanese literature, are not covered.

The way I read them also changed once. The first draft drew on selected sections of each paper, and an independent review found several footnotes and caveats I had missed that change the conclusions. Every item now in the references was read from start to finish, with an extraction record kept. Where I could read only an abstract, I say so in the text, do not use its numbers as support, and leave it out of the references.

The short version

"Strong" here means there is a meta-analysis and the direction is consistent. It does not mean the number will show up unchanged in a 5,000-word guide. The limitations section explains why.

Examples and explanations

Worked examples

A worked example lays out the problem, every solution step, and the final answer for the reader to follow. The alternative is to state the problem and have the reader solve it.

Christina Barbieri and colleagues' 2023 meta-analysis includes only studies of mathematics learning. The control groups had no worked examples: business-as-usual instruction or problem solving alone. Students who studied worked examples scored 0.48 standard deviations higher on average. More than nine in ten of the included manuscripts measured accuracy in solving problems.

The U.S. Institute of Education Sciences (IES) 2007 practice guide makes a recommendation in the same direction, rates the evidence as moderate, and states its scope as math and science problem solving. The body of that recommendation is more specific than its title, and four points are useful to a writer:

• Worked examples and problems for students to solve should alternate, with every other problem shown worked out. The guide describes one experiment that compared arrangements directly: placing six examples before six problems led to less learning than alternating them.
• After the concept has been taught, variability across problems (changing both the values and the problem formats) makes study more demanding but led to better performance on later tests.
• As learners gain expertise, the number of worked examples should go down.
• In some studies, worked examples without step-by-step explanations were the most effective.

Barbieri's meta-analysis also compares several ways of using examples (correct solutions only versus mixing in incorrect ones, initial learning versus practice). The authors say these are descriptive comparisons across studies and cannot be read as causal, so I do not turn them into advice.

What to do: for each main method in the article, include at least one example that states the conditions, every step, and the result. Follow it with a problem for the reader to solve, and make that problem differ from the example in more than the numbers.

Explanations next to an example: the direct meta-analysis I could not read

Authors writing a worked example usually annotate each step with why it is done. The meta-analysis that compares exactly that, worked examples with provided explanations against worked examples without them, is Jörg Wittwer and Alexander Renkl's 2010 analysis. The study exists, but I could not find a full text made public by its authors or publisher, so I do not cite its numbers or conclusions. Among the sources I could read, only two bear on it: the IES guide's remark in the previous section that in some studies worked examples without step-by-step explanations worked best, and the self-explanation meta-analysis below.

Kiran Bisra and colleagues' 2018 meta-analysis (I checked its numbers against chapter 2 of Bisra's doctoral thesis, which adapts the journal article) looks at the same question from the other side. Learners prompted to self-explain beat controls overall, g = 0.55. In the comparisons where the control group received a ready-made explanation, self-explaining still won, by a smaller margin and across only 6 comparisons. The authors also point out that this means a substantial share of the benefit is available from provided explanations.

Two conditions go with this analysis. It includes several inducement formats, among them multiple choice and fill-in-the-blank; writing things down is not a condition. And it excluded studies that bundled self-explanation with feedback, so "answer first, then see the answer" falls outside its scope.

So whether ready-made explanations help at all, the two sources above point different ways: the IES guide leans toward leaving them out, while Bisra and colleagues note that provided explanations can deliver part of the benefit. Having readers explain for themselves has support, though from few comparisons. My practice is to stop at the key step and ask the reader "why is this step allowed?" rather than add another paragraph of commentary; this is my inference.

Use concrete and abstract together, and write out the mapping

The IES guide rates "connect and integrate abstract and concrete representations" as moderate evidence. What it recommends is using both and making the correspondence between them explicit; it also says that using only abstract or only concrete representations leads to less flexible knowledge, and that concrete representations make initial learning easier but hinder applying what was learned to new situations. The guide mentions a technique called concreteness fading: learning starts with a concrete representation, and over time its key components are replaced by more idealized and abstract ones. I did not find a meta-analysis of that sequence. (Fyfe and Nathan's 2019 theory paper traces the idea to Bruner's 1966 work.)

Individual experiments do not all point the same way; the details are in "Where the sources differ" below. One thing to note here: Kaminski and colleagues' 2008 experiments directly tested "learn a concrete example first, then the abstract representation," and the group that learned only the abstract representation transferred better.

What to do: opening with a concrete scenario is fine, but the abstract form should appear in the same passage, with a statement of which thing in the scenario corresponds to which symbol in the formula. The basis for this sentence is the IES recommendation; no single experiment establishes it.

Putting two cases side by side for comparison is a neighboring practice. In the 2013 meta-analysis by Alfieri and colleagues, having learners compare two cases gave an overall effect size of d = .50; against studying the same two cases one after the other it was only .37. The largest effect came from asking learners to find similarities and giving the principle after the comparison (1.18), but all 29 comparisons in that cell come from three experiments in a single paper. In studies tested a day or more later, the effect was only d = .22.

State the misconception, then refute it

Refutation text typically states a common wrong idea, points out that it is wrong, and gives the correct explanation. Ordinary expository text does only the last.

Two recent meta-analyses cover it, both mainly comparing refutation text with text that does not refute. Noah Schroeder and Aurelia Kucera's 2022 analysis found g = 0.41. Robert Danielson and colleagues' 2024 analysis was preregistered, included more than twice as many studies, among them unpublished ones, and found g = 0.37. The primary studies in the two overlap considerably, so they cannot be counted as two independent pieces of evidence.

Four things call for a conservative reading:

• Neither tested what counts as a refutation text. The texts Schroeder and Kucera included vary in format; some only imply the refutation, and some raise the misconception with a question. They say outright that their study was not intended to examine how to design refutation texts. Danielson and colleagues say the three-part structure itself still needs systematic testing.
• After filling in possibly unpublished studies, Schroeder and Kucera's estimate drops to 0.28; the authors judge that this does not change the conclusion. Dissertations show the smallest effect in Schroeder and Kucera's analysis; in Danielson and colleagues' analysis the estimate for unpublished studies is smaller, and the difference is not significant.
• The studies Schroeder and Kucera included were almost all one-time interventions, and the longest text with a reported length was 1,542 words. The authors say they do not know whether the effect holds in long texts such as textbooks.
• Danielson and colleagues excluded studies that paired the text with discussion or interaction, and most included studies were not run in authentic instructional settings. They describe the effect as modest and do not recommend teaching science through text alone.

Here is an example of my own using gradient descent (untested):

Many people assume a smaller learning rate is always safer and only costs time. That is wrong. With a learning rate that is too small, the parameters barely move within a fixed training budget. The model sits close to where it started and looks as if it has converged, when it simply has not arrived.

What to do: pick one or two misconceptions your readers really hold, state each, and explain why it is wrong. Do not write only the correct version and hope readers notice the conflict with what they already believed.

Whether writing out a misconception can plant it in readers who never held it, and how to place the wrong claim and the correction, are covered in part 13.

Openings and structure

Learning objectives

"After reading this you will be able to do three things" is a common opening for a teaching article. This site's spec does not require objectives in the body, only that they be defined on a scope card before writing; but many articles list them anyway, so I checked. Faria Sana and colleagues' three experiments from 2020 are the only recent direct test I found, and the authors themselves say research on the question is limited.

Undergraduates read five short passages about mirror neurons and then took a 15-question applied test. Each question corresponded to a fact targeted by one of the objectives.

• The group with no objectives scored 47%, and the group with each passage's objectives placed right before it scored 55%, a significant difference. But participants had been told the objectives would help on the test and that they should look for the answers in the passages. In a footnote the authors mention another study without that instruction, in which the two groups did not differ.
• The group with all objectives listed at the start scored 53%, not significantly different from no objectives. Compared with each other, the massed and interpolated placements did not differ either.
• Another experiment rewrote the objectives as multiple-choice questions to guess at before reading; that group scored 67%, against 53% for the group reading ordinary objective statements.

Each passage was only 171 to 267 words. Objectives and prequestions targeted basic facts only, and the test did not cover content the objectives had not pointed to; the authors list that as a critical gap. In their limitations they write that recommending objectives be converted into questions is premature.

So what this set of experiments supports is: objective statements help unreliably, and where they sit makes no difference. Turning an objective into a question for the reader to guess at looks more promising, and the next section covers the meta-analysis of that practice.

Questions before the reading

The article on video covered Carpenter and Toftness's video experiment. The practice now has a meta-analysis. Quentin King-Shepard and colleagues' 2025 meta-analysis concludes: for content that was asked about in advance, g = 0.66; for content in the same material that was not asked about, g = 0.01. Counting only conditions with prequestions alone, with no feedback and no supplemental activity, the figure for questioned content is 0.60.

Several details are useful to a writer:

• Overall, unasked content neither improved nor got worse. There is also an earlier 1986 review by Christiaan Hamaker, which I could not read in a legal full text.
• The type of question matters. Conceptual questions, which take inference to answer, gave a small benefit for unasked content (g = 0.34); factual questions gave none; mixing the two types was negative. The authors say the effect is not large.
• Text versus audiovisual materials, questions at the start versus interspersed before each segment, and the amount of text made no significant difference.
• Viewing the questions without answering them did about as well as answering. But the authors caution that participants may have answered in their heads.

Steven Pan and Shana Carpenter's 2023 review adds two conditions under which unasked content also benefits: it is related to the question, or it comes before the answer in the material. The review also describes one online course study, which I later read in the original (Janelli and Lipnevich 2021): among the 399 people who took the tests, the three groups pretested before every module showed no detectable difference in post-test scores from the group without pretests, and the pretested groups completed modules as required at a lower rate. Two caveats. First, a pretested student counted as completing a module only after submitting both the pretest and the post-test, while the control group only had to submit the post-test, so "leaving the course" and "skipping the pretest" cannot be told apart. Second, "those who persisted scored higher" comes from an after-the-fact split by course completion, and the paper does not report the two groups' means.

Whether to give the answer right after the question is in "Where the sources differ" below.

What to do: pick the single most central question of the section and phrase it so that it takes some thought to answer. Do not ask about a peripheral fact. This is my inference, and there is evidence against it: in the few studies Pan and Carpenter review, prequestions requiring complex inference tended not to help, and they recommend prequestions for basic facts and concepts (see "Where the sources differ" below).

Headings

Research on headings is associated with Robert Lorch. Two experiments from 2013 by Lorch and colleagues compared two ways of communicating structure: a heading before each section, or the same information written as the first sentence of each section, not bold and not on its own line (called a preview sentence below).

• In the first experiment undergraduates read for understanding. The headings group recalled more subtopics (4.3 on average versus 3.2), and the groups did not differ in memory for detailed facts. This experiment had no control group with signals removed entirely.
• In the second experiment students outlined the text. Either headings or preview sentences beat having no signals, and there was no reliable difference between headings and previews.

The authors conclude that when readers are already looking for structure, previews work much like headings; when readers are simply reading to understand, previews are less noticeable than headings.

Anja Prinz-Weiß and Aline König's 2023 experiment had 51 university students read five science texts of about 500 words; half received a version with a heading before each paragraph. The headings here were questions, in bold on their own line. The headings group did better on the comprehension test and was less likely to overestimate how much it had understood; the difference on the memory test was not significant. The authors list as their first limitation whether the results extend to declarative headings.

Together: headings help readers grasp what parts the article has. Headings written as questions also helped comprehension in one small experiment.

An advance organizer is a framing passage, more general than the body, placed before it. The meta-analysis on this dates from around 1980 and I read only its abstract, which reports a small facilitative effect.

The reader's level decides how much assistance to give

This is the finding with the largest consequences for writing, and the hardest to act on: instructional assistance that helps novices can hurt experts. It is called the expertise reversal effect.

Leonard Tetzlaff and colleagues' 2025 meta-analysis finds two effects in opposite directions. Learners with low prior knowledge learned more from high-assistance materials (d = 0.51). Learners with high prior knowledge learned less from them (d = −0.43). Judging from those two averages, the authors call the effect asymmetric: giving novices assistance does more good than withholding it does for experts.

Applying this to writing involves two inferences of mine. First, "assistance" in this analysis is defined broadly: every manipulation of the instruction or task that is meant to ease processing counts. The authors' examples are animation versus static pictures and diagrams with or without labels, and the paper does not say how high and low assistance were coded. Mapping it onto "how much an article spells out" is my extension. Second, in more than half the studies "high prior knowledge" means the higher-scoring group of a sample divided by a test score, which is not the same as real experts; in those studies the disadvantage of assistance for the higher scorers was weakest.

Text coherence has an often-cited study pointing the same way, the 1996 experiments by McNamara and colleagues. I read only the abstract.

A public article cannot know who is reading. My approach is to write for novices by default and put the material only novices need into blocks that can be skipped: collapsed sections or links to another article. No study has tested whether collapsing or linking serves both kinds of reader.

The relationship between prior knowledge and learning, the details of the expertise reversal effect, and who benefits from more coherent text are covered more fully in part 12.

Segmenting and length

Günter Rey and colleagues' 2019 meta-analysis pools studies of multimedia materials. Cutting material into segments presented in sequence, or letting learners control the pace (either one counted), had small-to-medium effects on retention and transfer. The segmented groups also spent clearly more time.

I had hoped this analysis would answer "someone reading an article can already stop and reread, so does segmenting still matter?" It cannot:

• Whether learners could replay the material is not a significant moderator. On retention tests, segmenting was significant only when learners could not replay; on transfer tests the effect was larger when they could. The authors judge that the hypothesis "segmenting matters less when replay is available" was not supported.
• In the studies where learners controlled the pace, segmenting was not significant for retention and was significant for transfer.

The materials in this analysis are multimedia lessons that combine words with static or dynamic pictures, not plain text. I found no direct research on how much segmenting adds for long text. I also found no controlled experiment on how long a teaching article should be.

Where the sources differ

The following pairs of results point in different directions, or look as if they conflict while measuring different things. I list them side by side without picking one.

Whether to give the answer right after a prequestion. In King-Shepard and colleagues' meta-analysis, conditions that gave feedback with the prequestions scored highest on later repeats of the same questions (g = 1.25). The authors say outright that they hold back from a straightforward interpretation of that number, because it cannot separate the effect of questioning from learners remembering the answer. In the same table, feedback did nothing for unasked content. In Sana and colleagues' third experiment, the group given the correct answer right after each prequestion scored lower on the final test (58% versus 66%). Every question on Sana's final test corresponded to a fact the prequestions had asked about, recast as an application question; no question tested content the prequestions had not asked about. By King-Shepard's definition that is closer to a "repeated question" (assessing the same information), though King-Shepard's repeated questions were mostly worded identically to the prequestions. So on previously asked content, the two point in opposite directions: in the meta-analysis feedback scored highest, and in Sana's experiment the answer group scored lower. The difference may lie in whether the test question repeats the prequestion verbatim or recasts it as an application; that is my inference, and no study has compared the two directly. On unasked content, feedback did not help in the meta-analysis; Sana's experiment did not test that kind of question.

Whether viewing a prequestion without answering it helps. In King-Shepard and colleagues' meta-analysis, viewing and answering did about equally well. The IES guide describes a 1990 experiment concluding that answering is required. In Sana and colleagues' second experiment, replacing the question with a statement that included the answer made the benefit disappear. Richland and colleagues' Experiment 5 falls in between: the group told to memorize the questions without answering them got 78% of the asked content right, above the 63% of the group that only read, but below the 90% of the group that answered first.

Whether prequestions that require inference help. In King-Shepard and colleagues' meta-analysis, conceptual prequestions gave a small benefit for unasked content. In the few studies Pan and Carpenter's review covers, prequestions requiring complex inference mostly did not help.

Whether to pair worked examples with self-explanation prompts. In Bisra and colleagues' meta-analysis, self-explaining while studying worked examples is positive. In Barbieri and colleagues' meta-analysis, math worked examples paired with self-explanation prompts showed smaller effect sizes than those without; the authors say this is a comparison across studies, that most papers did not describe their prompts, and that it cannot be read as causal, and they cite two experiments with direct comparisons in which adding prompts helped. Bisra and colleagues also describe one experiment in which, with explanations available on demand, the group given only prompts beat the group given prompts plus on-demand explanations.

Abstract or concrete examples. Kaminski and colleagues found in 2008 that undergraduates who learned with an abstract representation transferred better, including against the group that learned concrete first and abstract second. Dragan Trninic and colleagues reran it in 2020 with the cover stories in all conditions changed to a children's game from another country and the icon for zero in the concrete condition redesigned; the concrete group learned much better at first, and the two groups did not differ on transfer to an abstract setting. The authors describe the concrete group's transfer advantage as partial and modest, and they acknowledge that without a randomized comparison of the old and new concrete examples they cannot be sure the original difference came from poorly chosen examples.

Whether headings help memory or comprehension. In Lorch and colleagues' experiment, headings led readers to recall more subtopics and made no difference for detailed facts. In Prinz-Weiß and König's experiment, headings were not significant on the memory test and helped comprehension. The two differ in control condition (section-opening previews versus no headings at all), in the form of the heading (declarative versus question), and in the tests. On memory for details, neither actually saw an advantage for headings.

Three things you can do tonight

Pick a teaching article you have written and change it as follows. It takes about an hour:

1. Find the most important example and add, after it, a problem for the reader to solve whose conditions differ from the example's.
2. Think of the wrong idea readers are most likely to bring with them, state it in the relevant paragraph, and explain why it is wrong and what actually happens.
3. Pick one section and open it with a question that takes some thought, for example "Guess first: if the learning rate is halved, how many times more steps does convergence take?"

How to write questions and feedback inside the article, how to handle wording, and what this research suggests for this site's writing spec are in the companion article.

Limits of this evidence

• No study directly tested self-learners reading long web articles. One synthesis includes experiments with long texts: the texts in King-Shepard and colleagues' analysis run to fifteen thousand words (counting only the passage right after the questions, with some word counts estimated), the median of the longest band being a little over two thousand, with text length not moderating the prequestion effect. But I did not read those experiments one by one, and none of them is a teaching article on the web. Carrying the other results over to long guides is my inference.
• Most materials are short. The longest text with a reported length in the refutation meta-analysis is 1,542 words. Sana's passages are under 270 words each, Prinz-Weiß's texts about 500 words, and Lorch's about 1,500.
• Participants are mostly college students, and most took part for course credit or pay. Self-learners who seek out an article have different motives.
• Large variation sits under the meta-analytic means. Study results differ widely and the mean is a summary; the numbers are in the appendix.
• Publication bias is only partly handled. Schroeder and Kucera's estimate drops after correction. In the worked-example meta-analysis Egger's test was significant, and a correction was applied. Bisra used only fail-safe N, which the Learning How to Learn article already explains tends to overstate robustness.
• The worked-example evidence is mathematics only, and almost all of it measures problem-solving accuracy. Extending it to "explaining a machine learning concept" is my extrapolation.
• Many comparisons are across studies: correct versus incorrect examples, replay or no replay, assistance for learners at different levels. The authors of the Barbieri and Rey analyses say outright that such comparisons cannot be treated as causal.
• Sampling bias is described at the top. No German-language research on instructional explanations is currently available to me in a legal full text.
• Eight points are my inferences: that results from short materials apply to long guides; asking the reader why at the key step instead of adding commentary; that Sana and the meta-analysis point opposite ways on answers because of verbatim versus applied test questions; mapping "instructional assistance" onto how much an article spells out; that skippable blocks can serve novices and experts together; phrasing prequestions so they take thought; the use of my gradient descent example as a model of refutation text; and the three things to do tonight. Each is marked in the text or listed here.
• Read as abstracts only and left out of the references: McNamara et al. (1996) on text coherence and Luiten et al. (1980) on advance organizers.
• Known to exist, no legal full text read: Wittwer and Renkl (2010), the meta-analysis of explanations in worked examples, and Hamaker (1986), the review of inserted questions. An earlier draft cited their numbers from third-party copies online; the source check found no version made public by the authors or publishers, so on 2026-10-14 all their numbers were removed and both were taken out of the references. Cromley and Chen (2025), the meta-analysis re-pooling Mayer-authored studies: the accepted manuscript I first read was obtained through a search service before its public date; it is scheduled to become public in NSF PAR on 2026-11-01, and I will restore the citation only once that version matches. Its numbers were removed on 2026-10-14.
• Read after publication: another prequestion meta-analysis, St. Hilaire et al. (2024), whose full text I could not obtain while writing this article and have since read. Asked content g = 0.54, unasked content 0.04 (no detectable difference), the same main result as King-Shepard and colleagues; it excluded studies that gave answers with the prequestions and studies that embedded the questions in the learning phase. King-Shepard and colleagues say several moderators disagree between the two, for reasons that are unclear. Janelli and Lipnevich (2021) was also read after publication; see the prequestion section above.
• Cited secondhand: the 1990 prequestion experiment described in the IES guide and the on-demand explanation experiment described by Bisra and colleagues; I did not read those originals. The experiment by Richland and colleagues and the two classroom studies described by Pan and Carpenter, and the arrangement experiment described in the IES guide (Trafton and Reiser 1993), were read in the original after publication, and the descriptions match.
• Gaps in what I could read: the page I obtained for Pan and Carpenter lacks the contents of its tables and figures; for most papers I read only the captions of figures.
• Not found: a synthesis on writing with analogies, a meta-analysis of concreteness fading, research on segmenting for plain text, and experiments on the right length for a teaching article.

Appendix: study designs and numbers

The body keeps one or two numbers per item. The rest are here.

Barbieri, Chawla, Miller-Cotto & Clerjuste (2023), Educational Psychology Review 35. Screened 8,033 abstracts; included 43 articles, 55 studies (2 of them quasi-experimental), and 181 effect sizes, mathematics only, from elementary school to college. Robust variance estimation, g = 0.48 (95% CI 0.36–0.60), I² = 93.72%. Egger's test was significant; after trim-and-fill, g = 0.44 (0.32–0.56). Cross-study moderators: correct examples only, β = 0.26 (p = 0.03), against a reference group of incorrect examples alone or combined with correct ones; paired with self-explanation prompts, β = −0.24 (p = 0.04); practice versus initial acquisition, β = −0.15 (p = 0.38). Of the 181 effect sizes, 69% came from conditions without prompts. The authors say all three are descriptive; the advantage of correct examples surprised them, because experiments comparing the two directly mostly found no difference or favored incorrect examples. Twelve articles tested interactions with prior knowledge, with mixed directions, and the authors summarize them descriptively only. Dosage ranged from under one class period (about 25 minutes) to a full academic year, and most studies did not report time. About half the studies were run in the United States.

Bisra, Liu, Nesbit, Salimi & Winne (2018), Educational Psychology Review 30. The numbers below were checked against chapter 2 of Bisra's 2020 doctoral thesis and match the journal version; the authors' discussion is in chapter 4 of the thesis. 64 reports, 69 effect sizes, 5,917 participants. g = 0.55 (0.45–0.65). By comparison condition: no additional explanation 0.67 (41 comparisons); provided instructional explanation 0.35 (6 comparisons, 573 participants). By task: studying text 0.79 (14), solving problems 0.48 (20), studying worked examples 0.36 (8); the between-group difference was not significant (p = 0.119). Of the 69 comparisons, 47 did not report time per group; among those that did, the self-explanation group took longer in 16 (0.72) and time was equal in 5 (0.41, from the thesis's Table 3; chapter 4 reports it as 0.36); the authors say the difference was not significant, and the between-group test across time categories gave p = .255. By total duration: under 30 minutes 0.71, over 2 hours 0.46 (6 comparisons), not significantly different. Participants were undergraduates in 42 comparisons. The inclusion criteria excluded studies that combined self-explanation with feedback.

Schroeder & Kucera (2022), Educational Psychology Review 34. Searched March 2020; 33 studies, 44 independent comparisons, 3,869 participants. For each comparison they took the latest test, preferring conceptual change measures. g = 0.41 (0.30–0.51), I² = 60.76. Egger's test was not significant; trim-and-fill added 10 studies on the left, giving an adjusted g = 0.28 (0.16–0.39). By publication type: journal articles 0.45 (36 comparisons), dissertations 0.11 (6, not significant), proceedings 0.73 (2); the between-group difference was significant. Participants were post-secondary in 30 comparisons (0.33). The length difference between texts did not moderate the effect (p = 0.26). 37 comparisons did not classify participants' prior knowledge. Another 30 studies could not be included because they did not report group sizes or the statistics needed.

Danielson, Jacobson, Patall, Sinatra, Adesope et al. (2024), Educational Psychologist; I read the accepted manuscript. Preregistered; 71 articles (53 published, 18 unpublished), 76 studies, 111 samples, 294 effect sizes, total sample 10,265, 1986 to 2021. In the posttest-only analysis, accurate beliefs g = 0.37 (67 studies) and inaccurate beliefs g = −0.38 (10 studies); the pretest-adjusted analysis gives 0.36 (49 studies) and −0.31 (6 studies); effects on positive emotions, negative emotions, and attitudes were not significant. Egger's test was not significant for the outcomes examined. Estimates from unpublished studies were smaller (0.22 to 0.31, against 0.39 to 0.40 for published), a difference that was not significant. None of the 26 moderators was significant at the 0.05 level; the authors say power was insufficient for some. The proportion of women in the sample was at p ≤ .10 in both analyses, with larger shares of women associated with smaller effects.

IES practice guide (Pashler et al., 2007). Evidence levels for its recommendations: spacing, interleaving worked examples with problem solving, combining graphics with verbal descriptions, and connecting abstract and concrete representations are all moderate; using quizzes to re-expose students to content and asking deep explanatory questions are strong; prequestions and the two recommendations on helping students judge what they have learned are low. "Low" is defined as expert opinion derived from strong findings or theories in related areas, or expert opinion buttressed by direct evidence that does not rise to the moderate level. Prequestions are rated low because they had not been tested with oral classroom instruction; the guide says experiments with written text are reasonably consistent, and it cautions that when readers can read selectively, prequestions reduce learning of content that was not asked about.

Kaminski, Sloutsky & Heckler (2008), Science 320. In Experiment 1, 80 undergraduates were assigned to four groups (the degrees of freedom in the tests correspond to 72 people, and the text does not explain the difference): one generic instantiation, or one, two, or three concrete instantiations. Training was equated, the transfer task was a novel concrete instantiation, and the generic group transferred better. In Experiment 2 participants were told directly how the elements of two concrete instantiations corresponded, and transfer still did not exceed chance. Experiment 4 compared "concrete then generic" with "generic only," and the latter did better. Trninic, Kapur & Sinha (2020), Cognitive Science 44. 38 participants per group; the cover stories were changed in all conditions. Initial learning: concrete 95%, abstract 70%. Transfer to an abstract setting 73% versus 78%, not significant; transfer to a concrete setting 95% versus 90%, significant before outliers were removed and not after; transfer to formal mathematics 78% versus 70%, not significant before outliers were removed and significant after (favoring the concrete group). The authors list five limitations, including the lack of a randomized comparison between the old and new concrete conditions and no measure of participants' mathematical ability.

Sana, Forrin, Sharma, Dubljevic, Ho, Jalil & Kim (2020), CBE—Life Sciences Education 19. Undergraduates at McMaster University; the test came 5 minutes after reading, with no delayed test. Experiment 1 had 164 participants: no objectives 0.47, objectives massed at the start 0.53, objectives before each passage 0.55. Only the last differed significantly from control (d = 0.49, p = 0.044); the two placements compared with each other gave p = 0.999. A separate study in footnote 1 omitted the instruction to attend to the objectives: control 0.49, objectives before each passage 0.52, not significant. Experiment 2 had 159 participants: multiple-choice prequestions 0.67, objective statements 0.53 (d = 0.84), fact statements that included the answers 0.57; accuracy on the prequestions themselves was 35%, with no feedback. Experiment 3 had 193 participants: correct answer (without explanation) given right after the prequestion 0.58, withheld 0.66 (p < 0.001); multiple choice and short answer did not differ. The final test used different questions from the prequestions, but each one corresponded to an objective's fact and tested its application; nothing outside the objectives was tested.

King-Shepard, Walker, Nokes-Malach, Carpenter & Fraundorf (2025), Educational Psychology Review 37. 55 records, 204 comparisons, about 12,000 participants, three-level model. Repeated questions g = 0.66 (95% CI 0.52–0.81, 181 comparisons); new questions g = 0.01 (−0.09 to 0.12, 175 comparisons). Repeated questions by presentation: prequestions alone 0.60 (110), with feedback 1.25 (significantly larger), with a supplemental activity 0.84 (p = 0.07), viewing without answering 0.65 (17, p = 0.71). New questions by question type: factual 0.002, conceptual 0.34 (18), mixed −0.40 (10); with feedback, new questions −0.04 (25). Text materials 0.67 and audiovisual materials 0.64 did not differ; questions at the start 0.65, interspersed 0.67; amount of text and duration, each in four bands, showed no difference, and the longest text band was 1,697 to 15,000 words. The repeated-question model showed signs of publication bias, with a corrected estimate of 0.68; the new-question model did not. Limitations the authors list: they did not analyze how closely questioned and unquestioned content were related, or where in the material the answers appeared.

Pan & Carpenter (2023), Educational Psychology Review 35. A narrative review; the page I obtained lacks the contents of its tables and figures. Studies it describes: Richland et al. (2009) had one group spend 2 minutes on 5 questions and then read for 8 minutes while another read for 10; the first did better on questioned content, including on a test one week later. Janelli and Lipnevich (2021) found no overall benefit in an online course, with pretested students more likely to drop out and those who persisted scoring higher. In two classroom studies (Carpenter et al. 2018, Geller et al. 2017), one prequestion plus a quiz after class showed no detectable difference from the quiz after class alone (Carpenter 2018, p = .06; in Geller 2017 the Bayes factor favored no difference). In Carpenter 2018's immediate end-of-class test, the prequestion group did better on asked content (d = .33), with no detectable difference on unasked content.

Janelli & Lipnevich (2021), Computers & Education 161. One MOOC, three pretest groups (no feedback, basic feedback, detailed feedback) against a control group with no pretests. The analysis covers 399 people who took the tests and completed at least one module, not everyone randomly assigned. Post-test composite scores did not differ significantly across the four groups (p = .42). Completion: 22.4%, 33.3%, and 31.3% in the three pretest groups, 50.5% in the control group. Among completers the pretest groups scored higher on the post-test (d = 0.46), an after-the-fact split by completion; the paper does not give the two groups' means.

Lorch, Lemarié & Chen (2013), Psicología Educativa 19. Texts of about 1,335 to 1,549 words on energy problems. Experiment 1 had 134 undergraduates and texts with 3 major topics and 13 subtopics; the headings group recalled 4.33 subtopics and the preview group 3.15 (partial η² = 0.07); no difference on fact questions. Experiment 2 had 120 participants outlining the text under no signals, previews, or headings: with the text present, the number of topics correctly included was 11.75, 15.50, and 16.20; from memory, 9.15, 10.40, and 12.35. The main effect of signals was significant; the difference between headings and previews was not (d = 0.40, p = 0.17). The authors caution that type of signal and typographical prominence are confounded and that their explanation needs further testing.

Prinz-Weiß & König (2023), Applied Cognitive Psychology 37. 51 university students, 25 in the headings group and 26 in the plain-text group; five natural science texts of 482 to 505 words and five to six paragraphs each, with a heading in question form before each paragraph in the headings group. The headings group did better on comprehension; the difference on memory was not significant (d = 0.52, p = 0.069). The plain-text group overestimated its comprehension and the headings group did not (between-group difference in bias d = 0.68); on another measure of judgment accuracy the groups did not differ significantly.

Tetzlaff, Simonsmeier, Peters & Brod (2025), Learning and Instruction 98. 60 experiments, 176 effect sizes, 5,924 participants, 1992 to 2024, median sample size 73. Low prior knowledge d = 0.505 (0.260–0.750), high prior knowledge d = −0.428 (−0.647 to −0.209); I² of 90.87% and 87.55%. Egger's tests were not significant. In 32 of the 60 studies participants were split into high and low groups by a test score; the disadvantage for high-knowledge learners was largest in the 8 studies that distinguished them by grade level. The effect for low-knowledge learners was especially weak in primary school (only 2 studies, too few to conclude anything, the authors say) and in language and humanities. The authors also pooled, study by study, the difference between the low-knowledge and high-knowledge effects, d = 0.971 (0.631–1.312); the difference in absolute size between the two effects (0.505 versus 0.428) was not tested, and the "asymmetry" is judged from the two means. A limitation the authors list: prior knowledge and assistance were both dichotomized, and the cut differs from study to study.

Rey, Beege, Nebel, Wirzberger, Schmitt & Schneider (2019), Educational Psychology Review 31. 56 investigations, 88 pairwise comparisons, multimedia materials; a study qualified by either segmenting or learner pacing. Retention d = 0.32, transfer d = 0.36. Replay, retention: not possible 0.40, possible 0.14 (not significant), between-group test p = 0.15; transfer: not possible 0.29, possible 0.55, between-group test p = 0.09. Learner-paced subset: retention 0.19 (not significant), transfer 0.45. By prior knowledge (retention): none 0.29, some −0.12 (not significant), high 0.73 (7 comparisons, 4 of them from one paper), the opposite of the authors' hypothesis. Learning time was longer in the segmented groups, with signs of publication bias for that outcome.

References

Each item was read from start to finish, with an extraction record kept; what I could not read is noted in parentheses.

• Barbieri, Chawla, Miller-Cotto & Clerjuste (2023), A Meta-analysis of the Worked Examples Effect on Mathematics Performance (full text on an author's site).
• Bisra (2020), Inducing self-explanation: A meta-analysis and experiment (doctoral thesis, Simon Fraser University), chapter 2 (discussion in chapter 4). The chapter adapts Bisra, Liu, Nesbit, Salimi & Winne (2018), Inducing Self-Explanation: a Meta-Analysis; the journal version has no legally available full text, and the numbers in this article were checked against the thesis.
• Schroeder & Kucera (2022), Refutation Text Facilitates Learning (supplementary materials not read).
• Danielson et al. (2024), The effectiveness of refutation text in confronting scientific misconceptions: A meta-analysis (accepted manuscript; supplementary materials not read).
• Pashler et al. (2007), Organizing Instruction and Study to Improve Student Learning (IES practice guide).
• Kaminski, Sloutsky & Heckler (2008), The Advantage of Abstract Examples in Learning Math (online supplementary materials not read).
• Trninic, Kapur & Sinha (2020), The Disappearing "Advantage of Abstract Examples in Learning Math" (the supplementary Data S1 was not read).
• Sana et al. (2020), Optimizing the Efficacy of Learning Objectives through Pretests.
• King-Shepard, Walker, Nokes-Malach, Carpenter & Fraundorf (2025), The Effect of Prequestions on Learning: A Multilevel Meta-Analysis (full text on an author's site).
• Pan & Carpenter (2023), Prequestioning and Pretesting Effects (the page obtained lacks the contents of tables and figures).
• Alfieri, Nokes-Malach & Schunn (2013), Learning Through Case Comparisons: A Meta-Analytic Review (read as the published version on co-author Schunn's page at the University of Pittsburgh LRDC, now offline and retrieved from the Wayback Machine; read after publication).
• Fyfe & Nathan (2019), Making "concreteness fading" more concrete as a theory of instruction for promoting transfer (read as the author manuscript in Indiana University's repository; read after publication).
• Trafton & Reiser (1993), The contributions of studying examples and solving problems to skill acquisition (the proceedings version on the first author's site; read after publication).
• Richland, Kornell & Kao (2009), The Pretesting Effect: Do Unsuccessful Retrieval Attempts Enhance Learning? (read as the published version on the first author's lab site; read after publication).
• Carpenter, Rahman & Perkins (2018), The Effects of Prequestions on Classroom Learning (read as the published version on the authors' site; read after publication).
• Geller et al. (2017), Prequestions do not enhance the benefits of retrieval in a STEM classroom (open-access published version in PMC; read after publication).
• Janelli & Lipnevich (2021), Effects of pre-tests and feedback on performance outcomes and persistence in Massive Open Online Courses (read as the published PDF on co-author Lipnevich's personal site; read after publication).
• St. Hilaire, Chan & Ahn (2024), Guessing as a learning intervention: A meta-analytic review of the prequestion effect (published version and table pages on the publisher's site, abstract and footnotes from the author manuscript in the Iowa State repository; read after publication).
• Lorch, Lemarié & Chen (2013), Signaling topic structure via headings or preview sentences.
• Prinz-Weiß & König (2023), Caption it! The impact of headings on learning from texts (supplementary material not read).
• Tetzlaff, Simonsmeier, Peters & Brod (2025), A cornerstone of adaptivity: A meta-analysis of the expertise reversal effect (supplementary materials not read).
• Rey et al. (2019), A Meta-analysis of the Segmenting Effect (columns in the study-by-study Table 1 were misaligned and not reconstructed row by row).
• Articles on this site: Writing Questions and Wording in a Teaching Article, Learning How to Learn, When a Teaching Article Should Use a Diagram, Pairing a Teaching Article with Video, and When a Reader Wants the Video Mid-Article.