Writing Questions and Wording in a Teaching Article: Evidence on Inserted Questions, Feedback, Jargon, and Writing Specs

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This article belongs to the series "Writing Articles That Teach." It covers the second half of the text itself: whether to put questions in an article, how to give the answers, how to handle wording and tone, and what stands behind the frameworks writers commonly use. The first half (examples, explanations, learning objectives, reader level) is in part 1. The two can be read separately. The last section checks this site's course-guide spec clause by clause and uses conclusions from part 1; the table gives each one in a sentence.

The site's Learning How to Learn article covers self-testing from the learner's side. This one is about what the writer can do: put the questions and the feedback into the article.

How these studies were chosen and read. 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. The studies that made it in lean clearly one way: English-language literature, college students, short materials, and studies whose full text I could obtain. The first draft drew on selected sections of each paper, and an independent review found several 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. That rule bites hard in this article: for feedback timing only one direct meta-analysis could be read in full, and for conversational tone the most direct meta-analyses are ones I could read only as abstracts or that have no legally available version yet.

The short version

Questions and practice inside the article

Inserted questions

Inserting a question every few paragraphs of a text is studied under the name adjunct questions. A classic summary is Christiaan Hamaker's 1986 review. The review exists, but I could not find a full text made public by its author or publisher, so I do not cite its numbers and use studies I could read in full instead.

The closest is the classroom quizzing meta-analysis in the next paragraph. When the exam repeated a quiz question, the effect size was 0.51; when the question was rephrased, 0.56; for content the quizzes did not cover, 0.32. The last cell is smaller, but the paper does not test the difference between those cells directly. The prequestions covered in part 1 show a sharper gap: 0.66 for asked content and 0.01 for unasked.

So choosing the questions amounts to choosing, on the reader's behalf, what is most likely to be remembered. That is my inference: one study is about classroom quizzes and the other about prequestions, and neither is about questions inserted after a passage in a web article.

The level of the question matters too, though the evidence is weaker. In the 2025 prequestion meta-analysis cited in part 1, conceptual questions that require inference gave a small benefit for unasked content (g = 0.34) and factual questions gave none; the authors call the effect modest. For questions asked after reading, I found no synthesis comparing higher-order and factual questions that I could read in a legal full text, so I draw no conclusion on that point.

Those numbers come from Chunliang Yang and colleagues' 2021 meta-analysis (full text on a co-author's site), which includes only studies of classroom teaching; quizzing raised achievement overall by g = 0.50. Against restudying the advantage was 0.33. Against strategies such as concept mapping and note-taking it was small, which the authors describe as only marginally better. Whether quizzes were high-stakes or low-stakes made no difference. Quizzes taken outside class, unsupervised, had smaller effects than those taken in class, a difference that is only marginally significant. The analysis explicitly excluded laboratory studies and online distance courses, so it still sits some distance from "a reader working through a web article alone."

What to do: the question after each section should ask about the one thing you most want readers to take away from it. Use "explain why" and "what happens if this condition changes" forms, not definition recall alone. The question-type half of 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 (those are prequestions, not questions after a section).

Whether to make readers answer first

Part 1 covered this: learners prompted to self-explain beat controls overall (Bisra and colleagues' 2018 meta-analysis, g = 0.55). The Lawson and Mayer experiments cited in the article on video point the same way: people who only read a provided explanation did not significantly outperform people who did nothing.

From that I had recommended putting "write your answer before reading on" on each question. After reading the sources in full, that recommendation has to be downgraded to a personal practice without direct evidence, for three reasons. Bisra and colleagues' analysis excluded studies that bundled self-explanation with feedback, and "answer first, then see the answer" is exactly that bundle. It includes several inducement formats, among them multiple choice and fill-in-the-blank, and it does not test writing things down. And in the prequestion meta-analysis, viewing the questions without answering did about as well as answering, though the authors caution that participants may have answered in their heads.

Part 15 looks at the same question from another angle: how accurately readers judge whether they have understood. In the meta-analysis it draws on, answering practice questions before judging made judgments somewhat more accurate, while only reading ready-made questions and answers showed no detectable help, so that article proposes folding answers by default and asking readers to answer before opening them. This article looks at learning, that one at judgment accuracy; the bases differ and so do the conclusions, and whether to change the spec is left to the site owner.

What the answer contains

Benedikt Wisniewski, Klaus Zierer, and John Hattie's 2020 meta-analysis sorts feedback into three kinds, with effect sizes rising in order:

• Reinforcement or punishment only: d = 0.24.
• Corrective feedback: 0.46.
• High-information feedback: 0.99.

Four caveats go with these three numbers. They pool controlled experiments with pre-post studies, and the latter show larger effects and are, by the authors' own account, less reliable. Only about a third of all the effect sizes were assigned to one of the three kinds. The kind was coded from the abstracts of the primary studies. And the bias test was significant, with no corrected estimate given.

"High-information" in this analysis is defined as the content of corrective feedback plus information at the self-regulation level. In their discussion the authors interpret it as telling students not only what was wrong but why, and how to avoid it next time. Mapping that onto "a sentence or two of reasoning after the answer" is my inference.

In Yang and colleagues' classroom meta-analysis, studies with feedback after quizzes had larger effect sizes than those without. That comparison is about whether feedback was given; it does not distinguish what the feedback contained. There is also a meta-analysis that compares feedback types in computer-based materials specifically (Van der Kleij et al. 2015). I read only its abstract, which points toward feedback with an explanation beating the correct answer alone.

What to do: where possible, write the answer to an end-of-section question as "the answer plus a sentence or two of reasoning." An open explanation question has no single answer; give a criterion.

When to give the answer

Should the answer sit right after the question or come later? The meta-analysis that directly compares immediate and delayed feedback found no detectable difference on average, and the other I read only as an abstract. I draw no conclusion here; the details are in "Where the sources differ" below. On whether the answer should be collapsed, I found no direct research.

Doing predicts scores better than reading

Kenneth Koedinger and colleagues' 2015 study analyzed logs from an online psychology course. One standard deviation more interactive practice went with a 0.44 standard deviation higher total on the weekly quizzes, more than six times the figure for watching more video or reading more pages.

Three conditions apply. The quiz questions were drawn from the item bank of the courseware that provided the interactive practice. On the final exam written by the instructor, the share of high scorers among students who only did more practice was no higher than among those who only watched more video; it took both to make a clear difference. And the data are observational, with no random assignment. The authors consider that their causal inference model supports a causal effect of practice while acknowledging the evidence is only initial; I treat it as correlational evidence.

Language and presentation

Readability formulas

Formulas such as Flesch–Kincaid estimate difficulty from words per sentence and syllables per word. Scott Crossley and colleagues' 2023 study had more than a thousand teachers compare about five thousand excerpts in pairs, asking which would be easier for students to understand, then used various formulas to predict the judgments. Traditional and newer formulas both correlated moderately to strongly and explained 23% to 34% of the variance. The same paper notes that Flesch–Kincaid was originally derived from 18 passages of Navy training manuals.

Three things limit how far this goes. The criterion is teacher judgment, not measured comprehension, and the teacher ratings themselves are noisy. The excerpts are English reading material intended for school classrooms, each under 230 words. And in the authors' own model, what best predicted the teachers' judgments were word-level features such as how common and how concrete the words are.

I found no synthesis of whether rewriting to a formula improves comprehension, and read no counterpart for Chinese technical writing. So my judgment is not to use a readability score as a pass mark; the study itself makes no such recommendation.

Jargon: adding a definition may not be enough

Olivia Bullock and colleagues' 2019 experiment had members of the public read three passages, three sentences each, about emerging technologies. Half read versions with jargon and half read versions with the jargon replaced by plain wording; crossed with that, half had definitions available as mouseover text on the jargon terms.

• Readers of the jargon versions reported clearly lower processing fluency.
• Having definitions made no difference to fluency.

The experiment measured how smooth reading felt. It did not measure comprehension or learning, and the participants were not students. The jargon versions packed 10 jargon terms into each three-sentence passage, a very high density. The experiment did not record how many people actually moved the pointer over a term to see its definition, so "the tooltip did not help" could mean readers saw it and still struggled, or that most never looked.

What is established: in this experiment, the versions with plain wording in place of jargon read more smoothly. Some articles on this site use a hover glossary. My practice is to explain key terms in plain words in the body where they first appear; the only basis for it is the one experiment above. The compromise of keeping the term and adding a plain sentence beside it was not tested in that experiment and is my inference.

Conversational tone

Rewriting material to address the reader directly (using "you") is called personalization in the multimedia learning literature. Jennifer Cromley and Runzhi Chen's 2025 meta-analysis re-pools the multimedia studies with Mayer as an author, including this principle; the authors' manuscript is scheduled to become public in NSF PAR on 2026-11-01, and I have not read a legally available version, so I do not cite its numbers.

A broader meta-analysis (Ginns et al. 2013) I read only as an abstract. It reports effects and notes that in studies with longer instructional time the effects were small and not significant.

There is currently no evidence on conversational tone that I could read in full, so I have not changed the voice of guides that take over half an hour to read. That is a reservation, not a conclusion: the source pointing to "no effect over long durations" is one I read only as an abstract, and the other meta-analysis has no legally available version I could read.

Interesting but irrelevant content

Educational psychology calls content that readers find interesting but that is irrelevant to the learning goal seductive details; an example of my own is a story about someone struck by lightning inserted into an explanation of how lightning forms. NarayanKripa Sundararajan's 2018 dissertation pools 54 comparisons: groups whose material included such content did worse, g = −0.43. The author ran a sensitivity analysis: of the 11 studies with effects below −1, 6 shared a co-author, and without those 6 the estimate was −0.28; the author says the overall effect may be slightly exaggerated and its size is difficult to ascertain. A separate journal article on the same topic, Sundararajan and Adesope 2020, I read only as an abstract; its numbers may differ. The 0.33 cited in the diagrams article is the journal version's figure as cited by Noetel, and it measures the effect of removing such content, so its sign is reversed; the two may not cover the same studies, and a different size is not a contradiction.

The dissertation's publication bias tests were also significant. In addition, 50 of the 54 comparisons were run in laboratories; the 4 run in classrooms gave −0.15, with no detectable difference, and the 17 studies rated high in quality gave −0.24. What can be said is the direction: interesting but irrelevant content did not help learning. How large the effect is in real classrooms or when reading an article is uncertain.

This site's spec has a rule that moves verification history (login tests, page-by-page checks, subtitle corrections) out of the body. The original reason was that readers could not get through it. Mapping that rule onto this research is my inference: the studies tested anecdotes and decorative pictures, not audit logs.

Typeface and screens

Two results concern what the page looks like and are worth recording.

Whether a slightly hard-to-read typeface makes people learn better was once a popular claim. The 2018 meta-analysis by Xie and colleagues concludes there is no effect on recall or transfer. A published critique, whose authors wrote both of the miscoded studies, later pointed out coding errors in it: on recalculation the transfer conclusion largely holds; for recall, spot checks of a few studies found numbers that did not match, the pooled effect was not recalculated, and the authors remain skeptical of the recall conclusion. I read Xie only as an abstract and the critique in full.

The screen-versus-paper comparison has fuller evidence. Pablo Delgado and colleagues' 2018 meta-analysis compared reading the same text in both media; comprehension on paper was better than on screen (g = −0.21), and the authors consider that size educationally meaningful. The gap appears for informational text and for mixed informational and narrative text; the 7 comparisons using narrative alone show none, and the authors caution that this cell has few comparisons. It is larger under time limits and small when readers pace themselves, where the confidence interval crosses zero. The paper advantage was larger in comparisons that required scrolling, but the difference from comparisons without scrolling was not significant, and the authors list it for future research.

A web article cannot change the fact that its readers use a screen. Self-paced readers may be affected less; that is my inference from applying a cross-study moderator result to web readers.

Non-native readers and translation

Nearly every article on this site has a Chinese and an English version, so I looked for this specifically.

Heleen Vander Beken and Marc Brysbaert's 2018 experiment had undergraduates whose dominant language was Dutch study short expository texts, half in Dutch and half in English, and tested them in the language of the text. On a true/false test the two groups scored the same. Asked to write down what they remembered, the group that read in English and wrote in English did much worse (d = 0.86).

The authors offer several explanations without settling on one: expressing oneself in a second language may be harder, or memory for a text read in a second language may be organized differently. The experiment had no condition of "read in English, answer in the first language," and the authors caution that switching languages between study and test may carry a cost of its own. So I do not recommend "ask readers to answer in their first language." What can be said is this: readers working in a second language did as well as native readers on recognition-type questions and were at a clear disadvantage when they had to produce the content themselves.

As for whether translating instructional material from one language to another affects learning, I found no controlled study. What the search returned were small studies of machine translation as an aid for foreign-language reading, meta-analyses of second-language glosses and vocabulary learning, and meta-analyses of English-medium instruction. None answers this question and I did not read them.

What stands behind practitioner frameworks

People who write technical documentation and design courses lean on three frameworks. I checked the basis of each, and the three are in different positions.

Diátaxis sorts documentation into tutorials, how-to guides, reference, and explanation. Its home page rests on the projects that have adopted it and three user testimonials. Its Foundations page opens by acknowledging that "It makes sense and it feels right" is not enough to ground a theory, then derives the four types from two dimensions, action versus cognition and acquisition versus application. Neither page cites an experiment or a user study. I also found no study comparing documentation written with and without it, though not finding one does not prove none exists. For now it is a clearly organized practitioner convention.

Backward design and alignment. Setting learning goals first, then assessment, then instruction comes from Wiggins and McTighe's Understanding by Design. I did not finish checking this one. Carnegie Mellon's Eberly Center page argues that objectives, assessments, and instructional strategies should align; the page itself cites no research. Ufuk Uluçınar's 2021 synthesis synthesizes qualitative findings only: one included study used an embedded experimental design and one mixed methods, and the synthesis takes only their qualitative parts. Its author concludes that the approach positively affects teachers' professional development and students' success, on the basis of themes drawn from interviews and documents, with no effect sizes. During screening, the synthesis excluded 18 studies that tested the model's effects quantitatively with experimental methods; it does not list them or report their results. I have not read those 18, so this article cannot conclude whether backward design works.

Bloom's taxonomy and verb lists. Many guides to writing learning objectives come with a table of which verbs belong to "understand" and which to "analyze." Claudia Stanny's 2016 study collected such lists from the top 30 websites in a search. Judging from the URLs in its appendix, about 23 are universities or community colleges, and the rest are commercial sites, a nonprofit, a military college, school districts, and a professional association; the paper does not classify the sites. Of 433 distinct verbs, nearly half appeared in two or more levels. Stanny concludes that verb lists function like a thesaurus and are useful for finding wording; which level an objective belongs to has to be judged together with the specific content written after the verb.

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.

Immediate or delayed feedback. Kandemir and colleagues' 2026 meta-analysis includes only studies in computer-assisted learning that directly compared immediate and delayed feedback with random or quasi-random assignment, 51 studies and 160 effect sizes, and found no detectable difference on average (g = 0.03); the 7 studies with delays of at least a day leaned toward delayed feedback but not significantly, and studies varied widely. I read Van der Kleij and colleagues' 2015 analysis only as an abstract, which says delayed feedback timing had a negative influence on effect sizes; there the effect size is feedback against a control, not immediate against delayed. The two answer different questions, so abstracts that look opposite are not necessarily in conflict.

Inserted questions and unasked content. In Yang and colleagues' classroom meta-analysis, unquizzed content also improved, but it is not split into content related or unrelated to the quizzes; in the prequestion meta-analysis, unasked content did not improve. The settings differ (classroom quizzes, mostly after learning, versus questions before reading), so this is not necessarily a conflict. Yang and colleagues offer several explanations, including that classroom content is interrelated and that repeated study-and-test cycles make students more engaged afterward; none of these was tested in that analysis.

Questions before or after the reading. Pan and Carpenter's 2023 review describes three studies that compared the two directly: two favored questions after the reading and one favored questions before. It also describes two classroom studies in which one prequestion plus a quiz after class did no better than the quiz after class alone. I did not read those original studies. Yang and colleagues' meta-analysis has a comparison of "pre-class" and "post-class" quizzes, but pre-class there means before the instructor's lecture, when students may already have read the assigned material, so it cannot serve as evidence on asking before any reading.

Whether a prequestion should come with its answer, and whether it has to be answered. The details are in part 1. On previously asked content, conditions with feedback score highest in the meta-analysis (the authors do not present that as a recommendation), while in Sana and colleagues' experiment the group given answers scored lower, so the two point in opposite directions; on unasked content, feedback did not help in the meta-analysis, and Sana's experiment did not test that kind of question. Viewing without answering did about as well as answering in the meta-analysis, while two other sources point toward answering being necessary.

Checking this site's course-guide spec

The spec for this site's course guides lives in course-guide-contract.md. The table maps its text-related clauses, as they stood in the working directory on 2026-10-14, to the research in both articles. The section containing "one question at the end of each section" ("Pairing video with the body") was added on 2026-10-13 and had not yet been committed when this was written.

The first draft made seven suggestions. After re-examining each, five remain, and each only adds something the spec does not yet say and that a fully read source supports:

1. Follow a complete example with a problem for the reader to solve, one that differs from the example. The spec already requires explanation questions or variation problems, but in the section on teaching by role; I suggest adding "follow the example with a problem" beside the definition of a complete example. The basis is the IES guide's recommendation to alternate, whose scope is math and science problem solving; using it for concept explanations is my extension.
2. Add a sentence on how to "point out common misconceptions": write the wrong idea down, then explain why it is wrong, and do not write only the correct version. The basis is the two refutation-text meta-analyses. They did not test whether particular steps are required, so no format is prescribed.
3. Add a sentence to "from a concrete problem to intuition and mechanism": the abstract form should appear in the same passage, with the mapping between the concrete scenario and the abstract symbols stated. The basis is the IES guide.
4. Where possible, give a sentence or two of reasoning with self-check answers, keeping the existing "or a criterion." This one is an inference: the feedback meta-analysis supports high-information feedback, and mapping that onto "answer plus reason" is my step.
5. Label each "design rationale" entry by what kind of basis it is. Of the seven current entries, three (NN/g, Karnad, per-section self-checks) already state their sample and limits. For the other four I suggest: the IES guide is an expert panel's guide with an evidence level per recommendation; Diátaxis and the CMU alignment page cite no research themselves; the backward design behind the CMU page has experimental studies I have not finished checking; and Anthropic's skill documentation is a vendor's practical guide about writing instructions, not learning research.

Two suggestions from the first draft are withdrawn:

• "Distribute learning objectives to the first line of each section": the spec never required objectives in the body, and the research shows placement makes no difference.
• "Add reader prior knowledge to the scope card": the scope card already has that field.

Research has no answer yet on five things, and I suggest the spec leave them unregulated for now:

• Whether a prequestion should have its answer beside it.
• Where end-of-section answers go and whether to collapse them.
• Whether the answer should follow the question immediately or come later.
• Whether to tell readers on the question itself to answer first.
• Rewriting an objective as a question for the reader to guess at. One laboratory's experiments (Sana et al.) support it, but the original authors say it is too early to recommend. The prequestion meta-analysis supports prequestions themselves and did not test turning objectives into questions; it also found that when the control group received related activities such as learning objectives, the relative effect of prequestions on unasked content was −0.23; however, the control-type moderator as a whole reached only p = .07, and the authors say in the text that the types did not differ significantly.

And three things my judgment is to leave out of the spec: a conversational-tone requirement, a readability-score threshold, and a Bloom verb-to-level table. The reasons for the first two are in the subsections above; a verb list can serve as a tool for finding wording, but the lists disagree with each other and are not fit for prescribing levels.

As of 2026-10-14, none of the five has been written into the spec or checked with a trial reader.

Three things you can do tonight

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

1. Move two of the self-check questions from the end of the article to the sections they belong to, and rewrite them as "why" or "what if this condition changed" (the question type is my inference; see the section on inserted questions).
2. Add a sentence or two of reasoning to each answer.
3. Find the three terms readers are least likely to know, and confirm that each has a plain-language explanation in the body where it first appears, not only in a tooltip or a glossary at the end.

Then have someone who has not read the article try it, and see whether they can answer the end-of-section questions.

Limits of this evidence

• No study directly tested self-learners reading long web articles. Carrying results from classrooms, computer-based materials, and short laboratory texts over to web guides is my inference.
• No synthesis of inserted questions that I could read in a legal full text. For the classic one, Hamaker's 1986 review, I found no full text made public by the author or publisher. Recent meta-analyses concentrate on prequestions and classroom quizzing; none deals specifically with questions placed in the middle of an article.
• The classroom meta-analysis describes a different setting from a web article. It excluded laboratory studies and online distance courses, and unsupervised quizzes outside class had smaller effects (a marginally significant difference). In an unsupervised web article, readers can skip every question; whether readers actually answer is covered in part 10: the large-sample answer logs come only from MOOCs, and no study measured readers of public articles.
• The feedback meta-analysis covers a very wide range, with high heterogeneity, pooled study designs, and a significant bias test left uncorrected; the authors say themselves that the overall figure is an average.
• Feedback timing and conversational tone have no conclusion. The one meta-analysis on feedback timing I read in full found no detectable difference on average, with few studies of delays of a day or more; for conversational tone I read the most direct studies only as abstracts, or they have no legally available version yet.
• The doing-versus-reading study is observational, and the quiz questions were drawn from the practice courseware's item bank.
• The jargon experiment measured self-rated fluency, with members of the public, very dense jargon, and no record of whether readers looked at the definitions.
• The readability study's criterion is teacher judgment, the excerpts are short, and they are English reading material for schools.
• In the screen-versus-paper meta-analysis, the great majority of participants come from four large-scale studies; the authors recalculated without those four and got almost the same result. The moderator analyses compare across studies.
• There is only one second-language experiment, with undergraduates who had good English, reading short texts.
• Sampling bias is described at the top: English-language literature, college students, short materials, studies with accessible full text. I searched no Chinese or Japanese literature.
• Nine points are my inferences: carrying research results over to web guides; that choosing the questions decides what is most likely to be remembered; using "why" and "what if" question types after each section; mapping "answer plus reason" onto high-information feedback; putting plain wording for key terms in the body; not using readability scores as a threshold; that self-paced readers are less affected by the screen; that verification history is equivalent to interesting-but-irrelevant content; and using the IES worked-example recommendation for concept explanations. Each is marked in the text.
• Read as abstracts only and left out of the references: the feedback study by Van der Kleij et al. (2015), Ginns et al. (2013) on conversational tone, Sundararajan and Adesope (2020) on irrelevant content, and Xie et al. (2018) on hard-to-read typefaces.
• Known to exist, no legal full text read: Hamaker (1986), the review of inserted questions. An earlier draft cited its numbers from a third-party copy online; the source check found no version made public by the author or publisher, so on 2026-10-14 all its numbers were removed and it was 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.
• Not read: the 18 experimental studies of backward design that Uluçınar mentions. Cited secondhand: the before-versus-after comparison studies described by Pan and Carpenter.
• Gaps in what I could read: the middle of the reference list in Yang and colleagues was not read line by line; 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: controlled studies of translated instructional material, an evaluation of Diátaxis, a synthesis on rewriting to readability formulas, and research on collapsing answers.

Appendix: study designs and numbers

Yang, Luo, Vadillo, Yu & Shanks (2021), Psychological Bulletin 147. Includes only studies in which the content was taught in a classroom, excluding laboratory studies and online distance education; 222 independent studies, 573 effect sizes, 48,478 students, g = 0.499. Of the 573 effect sizes, 195 come from a single class session. By control condition: no activity 0.610, fewer questions 0.465, restudying 0.330, other elaborative strategies 0.095 (p = 0.062). Tested content 0.512, untested 0.321. With feedback 0.537, without 0.374. In class 0.514, out of class 0.401 (p = 0.051). High-stakes 0.441, low-stakes 0.477 (not significant). Quizzes before the lecture 0.186 (34 effect sizes), after 0.536 (487). Matching quiz and exam formats 0.531, mismatched 0.399 (still significant). Facts 0.524, concepts 0.644, application in problem solving 0.453, with no significant difference among the three. A single class 0.385, longer than a semester 0.624. The authors used five methods to check publication bias and judged the risk small. The paper has no separate limitations section.

Wisniewski, Zierer & Hattie (2020), Frontiers in Psychology 10. 435 studies, 994 effect sizes, about 61,000 participants (the abstract says more than 61,000). All pooled, d = 0.55; after removing 35 extreme values, 0.48. Studies with a control group 0.42, pre-post studies 0.63. By feedback type: reinforcement or punishment 0.24 (39 effect sizes), corrective 0.46 (238), high-information 0.99 (42); type was coded from the abstracts of the primary studies. Egger's test was significant. The paper does not analyze feedback timing and did not include moderators such as learner proficiency or setting.

Bisra, Liu, Nesbit, Salimi & Winne (2018), numbers checked against chapter 2 of Bisra's 2020 doctoral thesis. 69 effect sizes, 5,917 participants, g = 0.55 (0.45–0.65); control with no additional explanation 0.67 (41 comparisons), control given a provided explanation 0.35 (6 comparisons). Studies combining self-explanation with feedback were excluded. Full numbers are in the appendix of part 1.

Koedinger, Kim, Jia, McLaughlin & Bier (2015), Learning at Scale. 27,720 registered students; 939 registered for the interactive materials and took the final. The dependent variable is the total weekly quiz score: the standardized coefficient for doing activities was 0.44; for watching video and reading pages, about 0.065 each. Share scoring high on the final: more practice only 16%, more video only 15%, more of both 31%. Limitations the authors list: counts were measured and time was not, and there was only one course.

Crossley, Heintz, Choi, Batchelor, Karimi & Malatinszky (2023), Behavior Research Methods 55. 4,724 English excerpts for use in grade 3 to 12 classrooms, selected to be 140 to 200 words each and actually 135 to 228; 1,116 teachers compared them in pairs, with each excerpt read 46 times on average. Scores computed from two halves of the rating data correlated at 0.63. Existing formulas mostly correlated above 0.50 with teacher ratings, the highest at 0.58. The authors' own 28-variable model explained 50.7%; it was fitted on the same corpus, and the authors note it may be overfitted.

Bullock, Colón Amill, Shulman & Dixon (2019), Public Understanding of Science 28. An online experiment with a non-representative sample; 650 took part and 640 were analyzed; 323 in the definitions condition and 317 without. Processing fluency on a 7-point scale: jargon 4.57, no jargon 5.27 (η² = 0.11); main effect of definitions F = 0.37 (p = 0.543), and the interaction was not significant either. Word count was held constant across versions. In one of the models the definitions condition significantly predicted support for the technology, which the authors do not explain. Limitations the authors list: comprehension was not measured; looking up a definition by mouseover adds a behavior of its own; and the mediation model uses cross-sectional data.

Sundararajan (2018), doctoral dissertation, Washington State University (a separate journal article on the same topic, Sundararajan and Adesope 2020, was not read; these numbers can be cited only as the dissertation's). 54 comparisons, 5,111 participants, material with seductive details against without: g = −0.43 (95% CI −0.55 to −0.31). Egger's test and the rank correlation test were both p < .01. Without the 6 studies sharing a co-author, −0.28 (no confidence interval given). Setting: 50 laboratory comparisons −0.46; 4 classroom comparisons −0.15 (95% CI −0.56 to 0.25, no detectable difference). The 17 studies rated high in quality gave −0.24; the paper does not give its rating rules. A single author did the coding, with no inter-coder agreement reported.

Delgado, Vargas, Ackerman & Salmerón (2018), Educational Research Review 25. 54 studies from 2000 to 2017: 38 between-participants (169,524 participants, 165,778 of them from four large-scale studies; excluding those four gives −0.22) and 16 within-participants (1,531 participants). Between-participants g = −0.21, within-participants d_c = −0.21. Time-limited −0.26, self-paced −0.09; informational text −0.27, mixed informational and narrative −0.30, narrative only 0.01 (7 comparisons). With scrolling −0.25, without −0.13, a difference that was not significant. These moderator analyses use only the between-participants data. Text length (split at 1,000 words), device type, and type of comprehension were not significant moderators. The paper advantage grew with publication year. Egger's test was not significant. Limitations: 10 eligible studies were not included (8 lacked statistical data, 2 had non-normal data), and heterogeneity was high.

Vander Beken & Brysbaert (2018), Bilingualism: Language and Cognition 21. 199 first-year psychology students at Ghent University took part; 4 whose dominant language was not Dutch were excluded, leaving 195 in the analysis; all had at least four years of high school English. The test language matched the text. True/false test: no difference between languages (d = 0.07). Free recall: d = 0.86.

Stanny (2016), Education Sciences 6. The sample is the top 30 websites returned by a search for "action words for Bloom's taxonomy." 30 lists with 788 entries and 433 unique verbs; 236 (54.5%) appeared in only one category and 197 (45.5%) in two to six, 3 of them in all six. No verb was placed in the same level by all 30 lists; the lists include different verbs, and the paper does not separate "not listed" from "placed in another level."

Uluçınar (2021), International Journal of Curriculum and Instructional Studies 11. 48 records found in 6 databases, 7 of them duplicates across databases. Screening excluded 18 studies that tested effects quantitatively with experimental methods. The author says 12 studies were included in the end, but the overview table has 13 rows; some of the included studies used mixed methods. The paper has no limitations section.

IES practice guide (Pashler et al., 2007). The two recommendations relevant here, using quizzes to re-expose students to content and asking deep explanatory questions, are both rated strong, each with conditions: quizzes should be closed-book, favor recall formats (short answer, fill in the blank), and include corrective feedback; deep questions presume students already have basic knowledge; prequestions are rated low, on the grounds that they had not been tested with oral classroom instruction.

References

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

• Yang, Luo, Vadillo, Yu & Shanks (2021), Testing (Quizzing) Boosts Classroom Learning (full text on co-author Rongjun Yu's site; the middle of the reference list was not read line by line).
• Wisniewski, Zierer & Hattie (2020), The Power of Feedback Revisited (the online appendix listing the studies was not read).
• Bisra (2020), Inducing self-explanation: A meta-analysis and experiment (doctoral thesis, Simon Fraser University), chapter 2. The chapter adapts Bisra, Liu, Nesbit, Salimi & Winne (2018); the journal version has no legally available full text, and the numbers in this article were checked against the thesis.
• Koedinger, Kim, Jia, McLaughlin & Bier (2015), Learning is Not a Spectator Sport.
• Pan & Carpenter (2023), Prequestioning and Pretesting Effects (the page obtained lacks the contents of tables and figures).
• Crossley et al. (2023), A large-scaled corpus for assessing text readability (correlations for individual formulas appear only in a figure and were not read).
• Bullock, Colón Amill, Shulman & Dixon (2019), Jargon as a barrier to effective science communication (online supplementary material not read).
• Sundararajan (2018), Seductive details: A meta-regression and empirical study (doctoral dissertation, Washington State University; institutional repository version).
• Kandemir, Esposito, Gurgand & Ramus (2026), A Meta-Analysis of the Impact of Feedback Timing on Learning Outcomes in Computer-Assisted Learning (read as the version the first author deposited in HAL; read after publication).
• Weissgerber, Brunmair & Rummer (2021), Null and Void? Errors in Meta-analysis on Perceptual Disfluency (open-access published version in PMC; read after publication).
• Delgado, Vargas, Ackerman & Salmerón (2018), Don't throw away your printed books (full text in the University of Valencia repository; the appendix tables of individual studies were not read).
• Vander Beken & Brysbaert (2018), Studying texts in a second language: The importance of test type (author version).
• Diátaxis and its Foundations page (retrieved 2026-10-13).
• Carnegie Mellon Eberly Center: Why should assessments, learning objectives, and instructional strategies be aligned? (retrieved 2026-10-13).
• Uluçınar (2021), Findings of Qualitative Studies on Understanding by Design: A Meta-Synthesis (text inside figures not read).
• Stanny (2016), Reevaluating Bloom's Taxonomy: What Measurable Verbs Can and Cannot Say about Student Learning.
• Pashler et al. (2007), Organizing Instruction and Study to Improve Student Learning (IES practice guide).
• Studies cited in the spec table whose details are written up in part 1: Barbieri et al. 2023, Schroeder and Kucera 2022, Danielson et al. 2024, Sana et al. 2020, King-Shepard et al. 2025, and Tetzlaff et al. 2025.
• Articles on this site: Writing the Examples and Openings of a Teaching Article, Learning How to Learn, and Pairing a Teaching Article with Video.