How to Order a Series of Teaching Articles: Prerequisites, Mixed Practice, Spiral Curricula, and Readers Who Skip Around

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This is part 18 of the "Writing Articles That Teach" series, in its fourth section, "after some time has passed." The earlier parts covered how much of the spacing effect survives in real courses and how to build review into an article. This one widens the frame to the whole series: when several articles sit in a row, how do you decide the order, should later parts come back to earlier ones, and what can the author do when readers don't read in order?

The question comes from how this site orders its series. The site has a series-planning procedure (series-curriculum-design). It asks you to first map the dependencies ("B only makes sense after A"), then order by five principles: visible before invisible, motivation before abstraction, one leap at a time, concrete to formal, and spiral deepening. Then you check each adjacent pair for a "cliff." The procedure's core principle is "order by the learner's journey, not by the professor's taxonomy of knowledge." Course guides have their own spec: one lecture per article, never split into two, and an assignment comes after the lecture it depends on. A series' order is this site's reading order, not the original course's lecture number. When an article belongs to a series, the previous/next links at the bottom of the page follow the series order. This series' own arc (what goes on the page, what readers do, what readers bring, time, community, evaluation) was set with the same procedure. The question here is how far research supports these decisions.

Part 12, on reader level, already used a study of course pacing to infer that each article in a series should state its own prerequisites. This article puts that inference back into the context of ordering and adds the evidence on ordering itself.

How sources were chosen, and their biases. I scanned the literature first, then picked twelve sources to read closely. For eleven I found a legitimately public full text and kept an extraction record.

On ordering there is a summary of ten experiments in preschool math, a randomized experiment in a university AI course, an experiment in a physics online assignment (a preprint), and a review of algorithmic sequencing. On coming back to earlier material there is a middle-school math randomized trial, a count of textbook problems, a meta-analysis of interleaved learning (a study that pools results across many studies), a conceptual review of spiral curricula, and one medical school implementation. On reader behavior there are two MOOC log analyses. For the remaining source on the list (a meta-analysis of an adaptive math program), and for a separate review of learner-chosen paths, I could not find a legitimately public full text. The sources lean toward English-language work, math and STEM content, and classrooms or MOOCs. None of them studies a blog series.

The short version

Ordering a series: is there a basis?

Prerequisites: can't learn it without, or easier with?

A learning trajectory is an approach from math education: split a topic into levels from low to high and assume that teaching one level at a time works best. Arthur Baroody, Douglas Clements, and Julie Sarama's 2022 review summarizes ten randomized experiments from their own project, all with preschool and kindergarten children, testing two assumptions of the approach.

The first assumption: for a child at level n, teaching n+1 and n+2 before the target level produces more learning than teaching only the target level. Four of seven experiments supported it. The other three detected no difference, and the authors judged them failures of execution (for example, the materials both groups used actually contained both levels), said they could not count as valid tests, and none of the three was published. Among the four supportive experiments, only one reports an effect size with a large sample: 152 preschoolers learning shape composition, effect size 0.55.

The second assumption: the same activities ordered by the trajectory produce more learning than the same activities in scrambled order. One of three experiments supported it (length measurement). The other two were on patterning; the ordered group improved but did not significantly beat the scrambled group. The authors concluded that in patterning, teaching the levels in order was not crucial, and suspected the trajectory itself was wrong, for example that one level should perhaps come after another. In their words:

"an LT approach is only as good as the LT it uses."

What helps most for ordering a series is not the tally but a distinction. Even in the supportive experiments, some control children reached the target without being taught the earlier levels. The authors therefore split earlier levels into two kinds: those that are only "strongly facilitative" and those that are "necessary." There is only one example of a necessary prerequisite: in an experiment with 15 children, 7 of the 8 who were taught the target without the prerequisite concept learned almost nothing. In another experiment, the children with the lowest entry level could hardly be taught except in order. The authors infer that the farther learners are from the target, the more instruction needs to be adjusted to their current level.

Three limits come with this distinction. The single necessary case has only 15 children and the paper is still under submission. The authors also say they cannot rule out another explanation: the prerequisite and target concepts may not be separable, and the in-order group won simply because it got training on the prerequisite concept, a larger total dose of related training. If so, the "necessary" reading falls apart. All participants are young children and the domain is early math; carrying this over to adults reading technical articles is my inference. The paper does not say which effect size (d or g) it reports.

Ordering by transition difficulty beat a historical order

Diego Rivera Garrido, Sverrir Thorgeirsson, and colleagues ran a 2026 experiment at ETH Zurich, the only study I found that directly compares two topic orders with random assignment in a university course. The course was a large AI course; the topic was diffusion models, with ten concepts (stochastic differential equations, Fokker-Planck, Langevin sampling, DDPM, and others) turned into two weeks of video material.

• The control group got the topics in the order they appeared in the research literature: sampling first, continuous-time mathematical foundations last. The authors say this matches how Stanford CS236 and MIT 6.S184 order them.
• The experimental group got an order from the authors' PATHOS method: first remove transitions that violate prerequisite relations, then have 12 raters score the cognitive load of each remaining transition, then use a minimum spanning tree to find a low-total-cost path so that directly related concepts are taught back to back.
• The core material was the same for both groups; only the transition segments differed.

The experimental group scored higher (62.6% versus 57.3%, d = 0.32), and a two-sided test was also significant. All 448 students in the course were assigned to the two groups; the analysis covers the 209 who sat the test and consented to the use of their scores. The test came about three weeks after the material started to be released, with no delayed test.

Looking at the paper's figure, transition by transition, every step in the control order is also among the edges left after the researchers removed prerequisite-violating transitions. The paper does not publish the full prerequisite structure. So the comparison is between two teachable paths, and the one with lower transition cost, teaching related concepts back to back, won. This is my reading of the figure; the paper does not say so. The authors hold back a lot themselves:

• The result may reflect weak spots in the control order rather than an especially good experimental order. Eight teaching assistants who reviewed both sets of materials beforehand split four to four in preference.
• The authors state plainly that they do not claim the same advantage against any strong order: "we also do not claim that PATHOS would produce a comparable advantage against an arbitrarily strong baseline instructional sequence".
• Raters disagreed a fair amount; changing a few ratings could produce a different order.
• Building a PATHOS order takes considerable time.

Concept first or theory first? An experiment without peer review

Benjamin Dringoli and colleagues' preprint (version 2, 2021; it exists only as a preprint) used online homework in first-year electromagnetism at McGill. The same topic was written as three pages: concept (qualitative explanation with a figure), theory (equations), and example (a fully worked calculation problem). Every student read all three pages; only the order differed, giving six orders. After the three pages came a review page where all three could be read again, then a test of calculation problems.

The planned comparison of the six orders found no order significantly better; the authors' section heading says exactly that. The authors then loosened the hypothesis and compared "what the first page was": students whose first page was concept gained more than those whose first page was theory, with posttest scores 4 percentage points apart. Under two other gain measures the difference was not significant, one of four assignments went the opposite way, and the paper reports no effect sizes. During the homework, the share of students who wanted an example next rose from 42% to 66%.

The experiment supports very little: in an online assignment of under five hours, putting the concept page first may help a bit, and the evidence is weak.

Algorithmic sequencing did not significantly beat fixed human-designed orders

If human-made orders are shaky, why not hand the job to an algorithm? Shayan Doroudi, Vincent Aleven, and Emma Brunskill's 2019 review covers 41 controlled experiments in which an instructional order was learned from student data with reinforcement-learning-style methods. They tallied the results by vote counting (how many studies were significant or not), with no pooled effect size.

Closest to "the unit order of a course" is the cluster that sequenced interdependent content, 8 studies. None significantly beat all baselines: 2 beat a random order but did not significantly beat orders designed by experts or heuristics; 6 detected no difference from fixed orders such as increasing difficulty, expert design, or a difficulty spiral. The authors' wording is that there is not yet evidence that algorithms order better, not that they have been shown useless. The 6 classroom studies were all K–12 math, and 2 of them were the authors' own experiments.

This does not mean order is unimportant. The authors' conclusion says:

"the order of content almost certainly matters for domains with interconnected content (like mathematics)"

The authors' judgment is that with typical amounts of data it is hard to find an adaptive order better than an expert's. In the same review, the most successful cluster sequenced independent items (for example, when to review flashcards): 11 of 14 studies beat their baselines, though the baseline in this cluster was usually only a random order (8 of 14). One more number to keep in mind: among studies with significant results, 71% compared only against a random order or against baselines not shown to work.

A related product is ALEKS. The background section of the PATHOS paper says such systems use knowledge space theory to assess a learner's current state and recommend next steps during instruction. Ying Fang and colleagues published a meta-analysis in 2019; the study exists, but I could not find a legitimately public full text. The Doroudi review does not mention ALEKS; based on its inclusion rule (policies with hand-set parameters were excluded), I infer that this kind of system falls outside its scope.

Should later parts come back to earlier ones?

The same problems, spread across worksheets and mixed

Doug Rohrer and colleagues ran a 2020 cluster-randomized trial in seventh-grade math classes at five Florida middle schools, randomizing by class. Four problem types (writing a proportional equation from a graph, solving inequalities, simplifying expressions, finding a radius from a circle's area) had 8 problems each, and both groups did the same 32 problems, only arranged differently:

• Interleaved group: eight worksheets, each with one problem of each of the four types mixed together, spread over about three and a half months.
• Blocked group: all 8 problems of a type on a single worksheet.
• Both groups finished with the same mixed review worksheet, followed by an unannounced test an average of 33 days later.

The interleaved group scored 61% and the blocked group 38%, and the interleaved classes did better for every one of the 15 teachers.

Note that this is not "teach first, then mix old problem types into later homework": the interleaved group had all four types on every worksheet from the first one, and the paper does not say when teachers taught each type or how that lined up with the worksheets. Reading it as "later parts of a series revisit earlier parts" is my inference.

Before carrying this over to a series, know that it bundles two things. The authors say it directly: "In short, interleaved practice guarantees spaced practice." Spreading one problem type over eight worksheets across more than three months is spaced practice in itself; this experiment does not separate interleaving from spacing. The authors also note that both groups did other practice outside the study, so what was really compared was a high versus low dose of interleaving. They list four caveats that might be critical: interleaved assignments take more time (all 15 teachers said the interleaved worksheets took longer); the benefit may be smaller when the test is close to practice; learners new to a skill may need some blocked practice first; and students saw the solutions and corrected every problem, so interleaving may need that kind of feedback to work.

A separate commentary by the same group counted practice problems in six US seventh-grade math textbooks (2012–2015 editions): about a tenth were interleaved, about eight-tenths blocked, and the rest unclassifiable. The books varied widely, from 7% to 31%. The exception is Saxon, with twice as many interleaved as blocked problems, but it no longer appears on the textbook adoption lists the authors could find. On how much interleaving there should be, the authors say "the optimal proportion is certainly unknowable" and argue only for at least a few interleaved problems per school day.

The interleaving meta-analysis: a narrower definition than you'd expect

Matthias Brunmair and Tobias Richter's 2019 meta-analysis is often cited for "interleaving works." The interleaving it studies is this: while learning categories, examples of different categories are presented mixed (for example, paintings by different artists alternating), compared with finishing one category before moving to the next, followed by a classification test. That is not the same thing as the order of a series, or as mixing old topics into review.

Overall g = 0.42, falling to 0.29 after correcting for possible publication bias. By material: paintings showed the largest effect; math tasks were positive; expository texts showed no detectable effect, with a positive point estimate but an interval crossing zero; words were negative, based on only 3 papers. A cross-study regression suggests interleaving helps more when categories resemble each other and members of a category differ a lot. This is a cross-study association, not an experimental manipulation, and it was no longer significant once the outliers were put back. About the expository text result, the authors note specifically that it "does not imply that interleaving is ineffective when used with these learning materials".

I read the authors' accepted manuscript and did not compare it word for word with the journal version. Retention intervals were coded only as under 20 minutes or longer, so this analysis cannot say whether the benefit of interleaving lasts for weeks.

Spiral curricula: almost no efficacy research

The spiral curriculum comes from Jerome Bruner's 1960 book The Process of Education: return to the same topic after a while, going one level deeper each time. "Spiral deepening" in this site's planning procedure is that idea.

Jo Ireland and Melissa Mouthaan's 2020 review (in an in-house Cambridge Assessment publication) compares the spiral with nonlinear curriculum models. They point out that Bruner's book itself offered no efficacy evidence ("the lack of evidence offered for the efficacy of the spiral approach"), that literature assessing the impact of spiral curricula is scarce, and they speculate that this means the spiral has largely been accepted without being tested. This is the two authors' observation, with no account of how they searched, so it supports "no evidence," not "doesn't work."

The review relays arguments on both sides, neither backed by data. Supporters list benefits such as reinforcement that aids retention, simple to complex, and logical sequence. The criticism comes mainly from a commentary on US elementary math textbooks; the two points most relevant to writing a series are that because the topic will come up again, each pass stays shallow and students never reach mastery, and that when visits are too far apart, the reinforcement weakens.

The only implementation with data I found is Anthony Maltagliati and colleagues' 2023 study at the University of Arizona College of Medicine. Its "spiral curriculum" was this: in the pre-clerkship weeks without exams, students came to class for an hour-long quiz on earlier material, and faculty then reviewed each question. That is closer to spaced retrieval practice than to Bruner's re-teaching at increasing depth. The comparison was the two earlier classes that did not have this review. Those two classes rated whether it would help them retain material; the class that went through it rated whether it did. The earlier classes averaged 8.2 (out of 10); the class that actually had it gave 5.0. Average licensing exam scores did not differ significantly across the three classes, but the classes differed in curriculum length and incoming background, and the authors themselves say there were too many confounds to draw a conclusion. In free-text responses, students who went through it wanted it to be self-paced, and said mandatory attendance crowded out other commitments. The study did not measure retention, so it cannot answer whether revisiting reduces forgetting.

Readers who don't read in order

Pacing flexibility gets used up

Tommy Mullaney and Justin Reich's 2015 study compares two runs of the same HarvardX humanities course: the first released content in sequence, the second put everything up at once. Part 12 already covers its main findings and numbers: learners use up whatever pacing flexibility the course offers, and even with sequential release only a minority keep pace. Here are just two points related to ordering.

First: the certificate rates of the two runs were similar, but the authors ran no test, and the runs differed in more than the release pattern, so this cannot be read as "release pattern doesn't affect outcomes."

Second, a finding the authors call incidental: every week, a group of people spent most of their time in the first two chapters, and for many students that was the only part they saw. On that basis the authors suggest that a course's first chapter summarize the key ideas of the whole course, rather than just introducing the first topic. The suggestion has not been tested.

Certificate earners also skip and jump back

Philip Guo and Katharina Reinecke's 2014 study analyzed server logs from four STEM courses on edX in fall 2012. Its main subject is differences by age and country; two side results bear on ordering, and both count only certificate earners (about a tenth of all students):

• On average, certificate earners in the four courses visited only 67% to 86% of the unit pages, skipping 22% on average. "Skipping" means never opening a page; opening it without finishing doesn't count, so this is a lower bound.
• Certificate earners jumped back to earlier units three times as often as non-earners. Of those backjumps, 54% went from a problem set or exam back to a lecture, and 30% from a lecture back to a lecture.

The authors guess that the backjumps were for looking up information needed to answer questions, but they also offer another explanation: students treating assessments as a list of the course's learning goals. The data can't tell the two apart. The study has no learning measure, so it can't be used to say that skipping content doesn't hurt learning, or that jumping back helps.

Letting readers choose their own path: nothing I can cite

A series on the web already lets readers choose which part to read and in what order. For the meta-analyses I found on the average effect of giving learners that kind of control, I could read only the abstracts or less. Katharina Scheiter and Peter Gerjets wrote a 2007 review of learner control in hypermedia; the study exists, but I could not find a legitimately public full text. So claims like "readers with low prior knowledge need a preset path and those with high prior knowledge don't" are not made here. The closest result in the sources I could read is that, in the Baroody experiments, the children starting lowest most needed instruction in order, but that compares teaching orders, not reader choice.

Where sources disagree

The following results point in different directions, or one paper says different things in different places. I list them side by side without picking a winner.

Does interleaving help in math? In Rohrer and colleagues' classroom trial, the mixed group led by a wide margin (d = 0.83). In Brunmair and Richter's meta-analysis, the pooled effect for math tasks was positive and significant (g = 0.34), yet in their practical recommendations the authors say they are reluctant to recommend interleaving for math tasks, expository texts, grammar rules, foreign languages, and words, which is more cautious than their own math result. The two define "interleaving" differently: Rohrer's is mixed practice problems plus spreading over more than three months; Brunmair's is mixed examples in category learning, mostly with short retention intervals. Rohrer and colleagues' trial is not in Brunmair's reference list.

Does the learning-trajectory evidence count as support? Baroody and colleagues' abstract says five of ten experiments were supportive, and the concluding sentence says the overall evidence "corroborates the efficacy and basic assumptions". Only a third supported the second assumption, and the one that did is marked "Yes/No" in the table; the paper does not explain what "/No" refers to.

Is concept first the best order? Dringoli and colleagues' conclusion says "The optimal sequence of content presentation is Concept first", while a section heading in the results says "No sequence provides a significantly better learning outcome than others". The abstract also says instructors' and students' preferred orders differ strongly; in the survey figures, both groups most often prefer orders starting with concept, the big difference is in preferred content type (undergraduates choose examples, instructors choose concept and theory), and no test was run.

Is the original course order a good enough baseline? In the Doroudi review, algorithmic orders did not significantly beat fixed expert-designed orders, and the PATHOS authors also say their method is not designed to beat orders refined over long teaching experience. Yet the control order PATHOS beat is, the authors say, consistent with how Stanford and MIT courses order the topics. Both can hold at once: typical amounts of data make it hard to learn a better order, while reordering once by expert-rated transition difficulty may still help. This is my inference.

Spiral review: imagined versus experienced. In Maltagliati and colleagues' study, the two classes that hadn't had the spiral review rated their expectation at 8.2; the class that had it gave 5.0. These are different classes answering questions in different tenses; the paper's practice points say medical students are "strongly in favor" of structured time-spaced repetition, which holds only for the hypothetical.

Does coming back to earlier material help? Rohrer and colleagues' classroom trial supports spread-out, mixed practice. The only implementation I found that actually quizzed students on earlier material at regular intervals is Maltagliati and colleagues' medical school course, where students who went through it rated it neutral, its effect cannot be judged, and retention was not measured. The designs are very different (problems mixed into every assignment versus a mandatory session every few weeks), so neither cancels the other.

Is releasing everything at once viable? The abstract of Mullaney and Reich's working paper says releasing all at once "may be a viable strategy"; the body's conclusion describes a tradeoff with costs on both sides and recommends neither.

Checking this site's practice

Here is this site's series-planning procedure and course-guide spec, item by item, against the sources above. "This site's choice" means no research directly supports it; it is our own decision.

What you can do

Each item lists its basis; where no research tested it directly, I say it is an inference or this site's choice.

1. When mapping dependencies, label each line "must" or "helps." "Must" means the later article makes no sense without the earlier one (for example, you can't follow backpropagation without knowing what a gradient is); "helps" means the earlier one makes it easier, but a couple of sentences in the later article are enough. Put every "must" earlier and link back to it at the top of the later article; cover every "helps" with a sentence or two in place so readers who jump in can still get through. Basis: Baroody and colleagues' distinction between necessary and facilitative (early-childhood math; the only necessary case is one 15-child experiment). Applying it to series for adults is my inference.

2. In later articles' self-checks, include one question where readers must first decide which article's method applies. For example, in part 5, ask a question where the reader first decides whether part 3's approach or part 5's fits, then give the answer and the reasoning. Basis: Rohrer and colleagues' classroom trial (middle-school math, combined effect of interleaving and spacing, students corrected every problem); applying it to later parts of a series is my inference. Readers may feel that mixed learning works less well: Part 15 covers this kind of misjudgment, but those experiments were category learning with paintings and bird photos, not mixed practice problems. The answer is included because the authors list feedback as a possibly critical caveat; carrying this to articles readers work through alone is my inference, and whether readers will do the question is covered in Part 10.

3. When you want to "come back and go deeper," have the reader answer a question instead of explaining the earlier material again. Basis: Rohrer and colleagues' classroom trial supports spreading and mixing the same problems; spiral re-teaching has no controlled experiments (Ireland and Mouthaan), and critics add that because the topic will come up again, each pass stays shallow. But the only implementation that regularly quizzed students on earlier material (Maltagliati and colleagues) has effects that can't be judged, and students disliked the mandatory format, so put the question in the article and let readers choose whether to do it. Choosing "answer a question" over the alternative is my inference.

4. When two orders both work, write each transition between adjacent articles as one sentence, "after reading A, what's still missing to understand B," and pick the path with less missing and related concepts back to back. Basis: the PATHOS experiment (one course, one topic, about a 5-point difference). The authors' method needs 12 raters, which one person writing a series can't do; estimating transition difficulty with one sentence is my simplification and has not been tested.

5. At the top of each article, say what it uses from which earlier parts, with links. Basis: the MOOC data from Mullaney and Reich and from Guo and Reinecke: readers jump around, skip, and go back to look things up. Extending this to blog series is my inference. Part 12 makes the same point.

6. In the first article or overview of a series, include a summary of the whole series' key points. Basis: Mullaney and Reich's suggestion (many people see only the first two chapters); the authors did not test it.

Limits of this evidence

• None of the studies is about article series or self-learners reading the web. The ordering studies are early-childhood math classes, videos in a university AI course, and physics online homework; the mixed-practice study is middle-school math; the reader-behavior data come from 2012–2013 MOOCs. Carrying all of it over to blog series is my inference.
• Each ordering claim rests on one or two studies. PATHOS is a single experiment at one school, in one course, on one topic, with an analyzed sample of only 47% of those assigned; Dringoli and colleagues' paper is a preprint without peer review; only five of Baroody and colleagues' ten experiments were published in journals.
• No delayed tests. PATHOS and Dringoli and colleagues measured performance shortly after instruction only; we don't know if the benefit lasts. Rohrer and colleagues tested about a month after review, the longest in this set; Brunmair and Richter coded retention intervals only as under or over 20 minutes.
• Interleaving and spacing are not separated. Rohrer and colleagues say outright that interleaving guarantees spacing; Brunmair and Richter say the two are to some extent impossible to disentangle.
• The MOOC studies have no learning measures. Mullaney and Reich measured certificate rates and activity; Guo and Reinecke measured page visits and grades; both are observational.
• Brunmair and Richter's numbers come from the authors' accepted manuscript, not compared with the published journal version; the manuscript itself has more than a dozen mismatches between text and tables, and this article uses the table figures throughout.
• Conclusions I can't draw: the average effect on learning of giving readers control; whether low or high prior-knowledge readers need a preset path; whether spiral curricula work; whether readers of teaching articles go in order and how long before they return. For the first two, I could read the meta-analyses and reviews only as abstracts or not at all; for spiral curricula I found no controlled experiments; for the last I found no studies, and this site has no traffic or reading-behavior analytics installed.
• My inferences and this site's choices: neither PATHOS order violated the prerequisite relations (my reading of the figure); expert orders being hard for algorithms to beat and PATHOS beating a top-university course order can both hold; applying the necessary/facilitative distinction to adult series; reading mixed practice as later parts revisiting earlier parts, and preferring practice over re-teaching when revisiting; ALEKS being outside the Doroudi review's scope; the concrete wording of items 1 through 5 in "What you can do"; and the rows marked "This site's choice" in the comparison table. Each is flagged where it appears.
• Known to exist, but no legitimately public full text found: Fang and colleagues' (2019) ALEKS meta-analysis (DOI) and Scheiter and Gerjets' (2007) review of learner control (DOI).
• Secondhand citations: Snider's (2004) criticisms and Harden and Stamper's (1999) advantages as relayed by Ireland and Mouthaan; earlier interleaving studies as relayed by Rohrer and colleagues; the forgetting rates cited by Maltagliati and colleagues. I didn't read any of the originals, and the forgetting rates cited by Maltagliati and colleagues are not used in the body.

Appendix: study designs and numbers

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

Baroody, Clements, Sarama (2022), Education Sciences 12(3), 195. Ten randomized experiments from one IES-funded project, all with preschool and kindergarten children. Three shared design features: random assignment; the control condition differs from the trajectory condition in only one defining feature; a pretest first places each child on the trajectory. Assumption 1 (one level at a time versus skipping straight to the target), 7 experiments: supported by Experiment 3 (152 preschoolers, shape composition, effect size 0.55, p = 0.016), Experiment 4 (26 kindergartners, addition and subtraction; the paper gives only multiple qualitative indicators of a gain of 24% or more, no effect size), Experiment 7 (291 kindergartners, early arithmetic, supported overall and at the target level, no effect size), and Experiment 10 (15 preschoolers, cardinality; procedural fluency effect size 1.3, p = 0.032; conceptual understanding 1.68, p = 0.016; under submission); Experiments 1, 2, and 9 (76, 180, and 20 children) were not significant, which the authors attribute to methodological problems. Assumption 2 (same activities ordered versus unordered), 3 experiments: supported by Experiment 8 (189 kindergartners, length measurement, effect size 0.32 against the comparison condition, marked "Yes/No" in the table); not significant in Experiment 5 (16 children, main measure effect size 0.238, p = 0.48) and Experiment 6 (48 children). In Experiment 5 the control group labeled patterns with letters from the start, which the authors think gave the control group two advantages. Child-level results in Experiment 10: of the 7 taught in order, 5 had some success on the target concept and 6 had success on the target procedure; of the 8 taught the target directly, 7 learned almost nothing, and the one who succeeded had the best pretest. The paper's Tables 2 and 3 have four cells summing to 16, which doesn't match the 15 children, so the in-text numbers are used here. The authors say Experiment 10 cannot rule out an alternative hypothesis: the prerequisite and target concepts are not distinct, and the in-order group won because it got more total counting-based cardinality training. The paper does not say whether the effect sizes are d or g.

Rivera Garrido, Thorgeirsson, Meier, Pizza, Goswami, Solano, Cotrini, Su (2026), ICER 2026. A preregistered classroom randomized controlled trial with a crossover design; the primary analysis uses only the first test, before the crossover. One AI course at ETH Zurich, November 2025 to January 2026. 448 students were randomized into two groups of 224; 221 sat the test and 209 consented to the use of their scores (100 experimental, 109 control), with no significant difference in attrition. The material was diffusion-model videos released over two weeks, about 111 minutes for the experimental group and about 114 for the control group; the programming-exercise videos were identical, and the non-programming videos differed only in transition segments. The complete directed graph of ten concepts has 100 possible edges, reduced to 24 after removing prerequisite violations; 12 raters not involved in the study (7 TAs from other AI courses, 5 PhD students) scored the transition load of each edge on a 7-point scale, with a mean standard deviation of 1.53. The test was 32 four-option multiple-choice questions, closed book, 45 minutes, written by the research team, Cronbach's α = 0.80, overall mean 59.6%. Primary test (preregistered, one-sided) p = 0.011, d = 0.322 (standard error 0.140); two-sided p = 0.021; Welch t(207) = −2.33, p = 0.010; Mann-Whitney U = 4547.50, p = 0.019. The paper does not give a confidence interval for d or group standard deviations. In exploratory per-topic comparisons, DDPM theory showed the largest difference (d = 0.62); each topic had only 2 to 4 questions, and the authors say these are only suggestive. The cognitive load survey was filled in by 55 volunteers after the crossover; the experimental material received lower intrinsic and extraneous load ratings (d about −0.22 and −0.31), which is not a comparison under random assignment. In interviews with 8 students, a control-group student described the content as "very fragmented", and 2 of 4 experimental-group students found the pace too fast. The paper is inconsistent about test timing (two places say "immediately," two say three weeks); the more plausible reading is three weeks after the material began to be released.

Dringoli, Kolosova, Rademaker, Wray, Choquette, Hilke (2021), arXiv:1910.00145v2, preprint. First-year Electromagnetism and Optics at McGill, two online assignments in each of 2017 and 2018; four datasets of 426, 437, 346, and 399 records; the two assignments in a year were done by the same students, and neither the number of unique students nor the size of each group is reported. Procedure: pretest → three content types, each read as one page in random order, with a quiz after each page → a review page with all content → posttest, completed within 5 hours. With Tukey correction across six orders, concept–theory–example versus theory–concept–example: the average of individual gains (ḡ) p = 0.03, and the gain computed from average scores (g) p = 0.08. Comparing by first page: concept first versus theory first, g p = 0.033 and ḡ p = 0.035; normalized change not significant (p = 0.24 in the text, 0.29 in the figure); with negative gains set to zero, not significant, and example first highest. Raw posttest scores: concept first 4 ± 2 percentage points above theory first, p = 0.01. In one of the four assignments (the first in 2018), theory first was highest, which the authors attribute to leaked questions. In 2018, 69 students got perfect pretest scores, which the authors attribute to students looking up answers online. Preference survey: 111 respondents, with numbers by role not reported. No effect sizes anywhere in the paper.

Doroudi, Aleven, Brunskill (2019), International Journal of Artificial Intelligence in Education 29, 568–620. Read as the author version. Citation tracking found 34 papers with 41 studies; inclusion required at least one instructional policy learned from student data, and hand-set parameters were excluded. Five outcome classes: significantly better than all baselines 21, better only for low-achieving students 4, better than some baselines 4, not significant 11, significantly worse 1. Paired-associate learning 14 (11 better), concept learning 7 (4 better), sequencing interdependent content 8 (0 better, 2 mixed, 6 not significant), sequencing activity types 10 (4 better, 4 better only for low-achieving students; all baselines were random or deliberately poor policies), goals other than learning 2. The 8 interdependent-content studies: two lab studies by Green and colleagues 2011 (Experiment 1: d about 3.9 against random, not significant against a heuristic; Experiment 2: the effect against random is recorded as "?", not significant against experts); 6 classroom studies whose baselines were increasing difficulty (3), expert (1), and difficulty spiral (2), with smallest-group sizes from 9 to 133. Among studies with significant results or aptitude-treatment interactions, 17 of 24 (71%) compared only against random or unproven baselines; this 24 differs by one from the 25 in the table, which the paper doesn't explain. Of 15 classroom studies, 3 were significant and 4 showed benefits only for low-achieving students. Appendix B is the authors' own unpublished fractions experiment (220 fourth and fifth graders): simulations predicted the new policy would score 0.31 to 2.23 points higher (out of 16); the actual posttest was 7.97 versus 8.12 for the baseline, and the difference in gains was not significant.

Rohrer, Dedrick, Hartwig, Cheung (2020), Journal of Educational Psychology, read as the author manuscript (ERIC ED595322); volume and pages not verified. A preregistered cluster-randomized controlled trial in one Florida district: 5 public middle schools, 15 teachers, 54 classes (28 interleaved, 26 blocked), randomized by class and balanced within each teacher. The course excluded students who took algebra early and those who failed the previous year's state math test. 856 of 1,103 students consented; 787 were analyzed (398 interleaved, 389 blocked). No pretest; sixth-grade state test scores were similar across groups. The practice phase averaged 103 days, the review worksheet came 10 days later, and the test 33 days after that: 16 new problems, blocked by type. Interleaved 60.7% (SD 28.6), blocked 37.6% (SD 27.3), d = 0.83 (95% CI 0.68–0.97), computed on student-level data without adjusting for clustering; in a multilevel model controlling for teacher, the fixed effect of interleaving was 22.17 percentage points (SE 2.47). By teacher, d ranged from 0.23 to 1.48. Effect sizes by problem type ran from 0.86 to 0.34, which the authors say are confounded by scheduling. All 15 teachers returned the survey: all 15 said the interleaved assignments took more time; 5 disagreed with "I could easily create my own interleaved assignments." A pilot study with 83 students found d = 0.97.

Rohrer, Dedrick, Hartwig (2020), Educational Psychology Review 32, 873–883, read as the author manuscript (ERIC ED611830). A commentary that includes a count of problems. The sample: the seventh-grade books of six series that appeared on the adoption lists of all four states checked (California, Texas, Florida, North Carolina) and that an assistant could obtain (2012–2015 editions), 13,505 problems in total. Coding: a problem counted as blocked if it was the first problem in an assignment devoted to the previous lesson, or relied on the same skill as the problem before it; problems not clearly meeting either were counted as interleaved; unclassifiable ones were marked ambiguous. A second rater coded 1,792 problems, intraclass correlation .97. Each book averaged 1,814 blocked and 219 interleaved problems, more than eight blocked per interleaved. Working back from the averages, I get about 9.7% interleaved and 9.7% ambiguous, and about 81% blocked. Interleaved share by book: Big Ideas Math 9%, Connected Mathematics 31%, Glencoe 7%, Go Math 8%, Holt McDougal 8%, SpringBoard 7%. Saxon Math Course 2: 1,491 blocked and 3,016 interleaved; it does not appear on the adoption lists the authors found, and the reason given is their guess. The authors' stated limits: many textbooks were excluded, consumable workbooks were not included, teachers may supply interleaved assignments from elsewhere, and only US seventh-grade books were examined.

Brunmair and Richter (2019), Psychological Bulletin, read as the authors' accepted manuscript. A multilevel meta-analysis with searches through June 2018: 59 papers, 158 samples, 238 effect sizes, 8,466 participants; 173 effect sizes come from university-student samples. By material: paintings g = 0.67 (k = 70), naturalistic photographs 0.35 (19), artificial pictures 0.31 (63), expository texts 0.21 (25, p = .119, 95% CI −0.06 to 0.47), mathematical tasks 0.34 (45, p = .005), words −0.39 (13, p = .005), tastes 0.57 (3, not significant). The 25 expository-text effect sizes come from 7 papers, 15 of them from two (one on immune and reproductive system texts, one a troubleshooting simulation); words come from only 3 papers. Overall I² = 77.3%. After trim-and-fill, overall g = 0.29. Meta-regression: within-category similarity has a negative coefficient and between-category similarity a positive one, still significant after adding material type, and neither significant once the 12 outliers are put back. No moderating effect was detected for retention interval, retention versus transfer test, simultaneous versus sequential presentation, or publication status. A supplementary analysis of inter-item timing (k = 17): immediate succession g = 0.73, temporal spacing 0.22 (not significant), distractors in between 0.51. Text and tables disagree in more than a dozen places; for example, the discussion says interleaving is effective only with immediate succession, while the distractor condition was also significant in the results. This article uses the table figures throughout.

Ireland and Mouthaan (2020), Research Matters 30, 7–11, Cambridge Assessment. A conceptual review with no methods section and no data of its own, about subject curricula across grade levels. All advantages are relayed from Harden and Stamper (1999): reinforcement, simple to complex, integration with the rest of the curriculum, logical sequence, and higher-level objectives. Most disadvantages are relayed from Snider's (2004) commentary on US elementary math textbooks: superficial understanding, shallow treatment because topics will return, lost motivation from repeating what students already know, equal time for concepts of unequal difficulty, compressed time for effective learning, and weakened reinforcement when visits are too far apart. Nonlinear models such as network and lattice models likewise have no efficacy data, and the authors say they risk overloading learners.

Maltagliati, Paree, McIntosh, Moynahan, Vanderah (2023), Medical Education Online 28(1), 2167258. A single-school, non-randomized historical comparison. Classes of 2020, 2021, and 2022 (132, 120, and 125 students); only the class of 2022 received the intervention: 500 board-style multiple-choice questions written by the authors, delivered in 1-hour in-class sessions of 10 to 20 questions during non-exam weeks, ungraded, with faculty reviewing each question afterward, 32 sessions in all. The class of 2020 had a 24-month pre-clerkship curriculum, the later two 18 months; incoming GPA and MCAT rose class by class. Survey response rates were 36%, 45%, and 32%. The item on whether the spiral curriculum would help (earlier classes) or did help (intervention class) retain material: 8.2, 8.2, 5.0 (p < 0.000005); the item on having retained most material from earlier blocks: 5.0, 4.6, 4.2 (p = 0.15); USMLE Step 1 class means 224, 229, 227 (p = 0.21). The standard deviations in the abstract differ from the table by 0.1; this article uses the table.

Mullaney and Reich (2015), L@S '15, 185–194. Numbers are from the authors' public HarvardX working paper (2014); the tables in the published version were not compared. For the course, how the two runs differed, and the share of learners keeping pace, see the appendix of Part 12. Used additionally here: certificate rates (share of active students) of 0.056 for the sequential run and 0.057 for the all-at-once run, with no test; in the logistic regressions, weeks active is a stronger predictor than weeks on track. The authors' stated limits: non-random, a single humanities course, no learning measure.

Guo and Reinecke (2014), L@S '14. Four edX courses from fall 2012 (MIT 6.00x, Harvard PH207x, Berkeley CS188.1x, MIT 3.091x): 140,546 students in total, 14,645 certificate earners; the certificate threshold was usually around 60%. A unit (learning sequence) is one web page: a lecture, or a problem set or exam. Average share of units visited by certificate earners: 3.091x 67%, PH207x 77%, CS188.1x 81%, 6.00x 86%. Backjumps (jumps to an earlier-released unit, divided by units visited): certificate earners 1.04 (SD 0.62), non-earners 0.3 (SD 0.4). Types of backjump (average across four courses): assessment to lecture 54%, lecture to lecture 30%. Older learners covered more; those over 40 made 5% to 12% more lecture-to-lecture backjumps than those under 20 (significant in three of four courses). The study's conclusion presents the 22% as a result for all 140,546 students, but it was computed only on certificate earners.

References

Every entry was read in full and has an extraction record; parts I could not read are noted in parentheses.

• Baroody, Clements & Sarama (2022), Lessons Learned from 10 Experiments That Tested the Efficacy and Assumptions of Hypothetical Learning Trajectories (published version, CC BY; tables checked against the PDF indexed by ERIC).
• Rivera Garrido, Thorgeirsson, Meier, Pizza, Goswami, Solano, Cotrini & Su (2026), PATHOS: A Pedagogical Method for Sequencing Instruction in Multi-Foundational Machine Learning (read as the ACM typeset version on a co-first author's ETH page; the GitHub supplementary materials and preregistration were not read).
• Dringoli, Kolosova, Rademaker, Wray, Choquette & Hilke (2021), The impact of content sequencing on quantitative problem-solving: A case study in Electromagnetism using an online learning platform (arXiv:1910.00145v2, preprint, not peer reviewed).
• Doroudi, Aleven & Brunskill (2019), Where's the Reward? A Review of Reinforcement Learning for Instructional Sequencing (read as the author version on the first author's UCI page; the middle part of the reference list was not checked entry by entry).
• Rohrer, Dedrick, Hartwig & Cheung (2020), A Randomized Controlled Trial of Interleaved Mathematics Practice (read as the author manuscript indexed by ERIC; materials and preregistration on OSF were not read).
• Rohrer, Dedrick & Hartwig (2020), The Scarcity of Interleaved Practice in Mathematics Textbooks (Educational Psychology Review 32, 873–883; read as the author manuscript indexed by ERIC).
• Brunmair & Richter (2019), Similarity matters: A meta-analysis of interleaved learning and its moderators (read as the accepted manuscript on the authors' institutional site, not compared with the published journal version; Appendix A and the electronic supplements are not in the manuscript).
• Ireland & Mouthaan (2020), Perspectives on curriculum design: comparing the spiral and the network models (Research Matters 30, published version on the publisher's site).
• Maltagliati, Paree, McIntosh, Moynahan & Vanderah (2023), Development and evaluation of a pre-clerkship spiral curriculum: data from three medical school classes (published version, CC BY; the image for Figure 1 was not seen).
• Mullaney & Reich (2015), Staggered Versus All-At-Once Content Release in Massive Open Online Courses: Evaluating a Natural Experiment (numbers from the authors' public HarvardX working paper; tables in the published version not compared).
• Guo & Reinecke (2014), Demographic Differences in How Students Navigate Through MOOCs (read as the final conference paper on the first author's institutional site).
• On this site: Writing a Teaching Article for Readers at Different Levels, Writing the Examples and Openings of a Teaching Article, Writing Questions and Wording in a Teaching Article, Do Readers Answer the Questions in an Article, Do Readers Know Whether They Understood?.