1. The policy problem: lost learning and unequal recovery

After the closure of schools because of COVID-19, systems faced a policy problem: a learning loss that was measurable, persistent and unequal. High-dosage tutoring was offered as a response because the prior experimental literature placed it among the interventions with the largest effects. That promise holds only as a programme with a dosage, a mode of delivery, a specification of who tutors and a cost.

Empirical finding. Wisenöcker et al. (2025) meta-analysed 763 effect sizes from 103 studies in 45 countries (April 2020 to June 2022). The mean loss was Cohen’s d = −0.20 (standard error = 0.04, p < 0.001). The only significant moderator was domain: losses were larger in mathematics. They were also observed more than two years after the onset. That average is not a Mexican national figure.

Empirical finding. Donnelly and Patrinos (2022) identified eight studies between March 2020 and March 2021: seven found loss in at least some of the participants; one of those seven also found gains in a subgroup; the remaining study found gains. Four observed increases in inequality.

Source limitation. The systematic review by Dela Cruz et al. (2025) of learning loss and recovery from the COVID-19 pandemic is included only for the object of its title. No magnitude, direction or coverage is asserted.

Empirical finding. Angrist et al. (2021) model loss and pathways to recovery with early-grade reading assessments in Ethiopia, Kenya, Liberia, Tanzania and Uganda. The data suggest a loss of half a year to more than one year. A deficit in grade 3 could translate into 2.8 years of lost learning by grade 10. The authors argue that targeted instruction and structured pedagogy could improve learning even above pre-COVID-19 levels.

Empirical finding. Singh et al. (2026) follow a panel of approximately 19,000 primary-school-age children in rural Tamil Nadu. In December 2021 the deficits were approximately 0.73σ in mathematics and 0.34σ in language, relative to students of the same age in the same villages in 2019. Two thirds recovered in the six months after reopening. The loss was regressive and the recovery progressive. A government out-of-school remediation programme contributed approximately 24% of the cohort recovery.

Source limitation. The longitudinal study by Schult et al. (2026), using mandatory large-scale assessments of how schools recover from pandemic learning loss, is cited only for the object of its title. No trajectory or speed of rebound is asserted.

Empirical finding, from the policy context. Kraft et al. (2026) document that United States public schools undertook an unprecedented effort to expand tutoring after COVID-19, supported in part by the large effects of earlier meta-analyses. That expansion turns the question into one of programme evaluation: what impact can be expected at scale, with independent tests and the dosage actually delivered.

The question of this review is explicit: what effects of high-dosage tutoring do recent meta-analyses and randomised trials document, under which components of dosage and according to who tutors, and why do those effects shrink at scale? The object is compulsory education (PreK–12). Each claim is labelled as an empirical finding, a conceptual framework or a design inference. No data for Mexico or for Latin America are invented.

2. What high-dosage tutoring is and is not

Conceptual framework. High-dosage tutoring designates here a design package, not a label: frequent sessions, several a week; groups of one to three or four; placement inside the school day; a stable and trained tutor; and material aligned with the curriculum or with a structured sequence. No study uses exactly that list as a legal definition.

Empirical finding. Nickow et al. (2024) find that effects tend to be larger with teacher or paraprofessional tutors, in earlier grades, on at least three days a week and during school. A programme that is called tutoring and is offered once a week, outside school hours, with large groups and a rotation of tutors, is not the same causal object. Kortecamp and Peters (2024) operate two or three times a week, with specially trained tutors and a sequence from letters to stories. Hamlin et al. (2026) operate groups of 2:1 or 3:1 in high schools. de Ree et al. (2023) implement high-dosage tutoring in three primary schools in a low-income neighbourhood in the Netherlands. High frequency, a small group, a trained tutor and anchoring in the school are the recurrent features.

Finseraas et al. (2026) function as a low-dosage counter-example. Their small-group mathematics instruction for students aged 7 to 9 had a lower dosage, was directed at the full population and used pull-out with fixed instructional time. Empirical finding. There are no significant effects 3.5 to 4.5 years later; the point estimates suggest a fade-out of approximately 47% to 58%, depending on the specification. An intervention that differs in dosage and in target is not a test of the intensive package.

Conceptual framework. Distinguishing objects avoids averaging distinct interventions. What produces the effect is not that “tutoring” exists on the organisational chart, but that a dense dosage is delivered, within the timetable, with continuity of tutor and with a small group.

3. Method: critical narrative review with a screening flow

Methodological note. This is a critical narrative review, not a meta-analysis of our own. There is no double coding and no pooled estimation of effects. The base was the Crossref REST API on 21 October 2026: 16 queries of 60 rows, journal articles from 2021, on intensive or high-dosage tutoring, meta-analyses and trials, online tutoring, peer tutoring, loss and recovery, teaching at the right level, the National Tutoring Programme and tutoring in developing countries. The lexical screening is in screen.py; the inclusion of 24 sources was a manual selection.

Screening stepRecords
Crossref queries (rows per query)16 (60)
Unique records verified (2021–2026)382
Excluded for year out of range0
Excluded: corrections, errata or reviews0
Excluded: journals of doubtful editorial quality40
Excluded as out of scope107
Eligible after screening235
Included by manual selection24
With a usable abstract20
Cited by title only4
Latin American studies included0
Studies from low- or middle-income countries2
Table 1. Crossref screening flow (2021–2026). Out of scope: higher and medical education, private tutoring (except one contrast meta-analysis), anxiety, robots, protocols and titles unrelated to tutoring or recovery. Chain 382 − 0 − 0 − 40 − 107 = 235.

Of 382 unique verified records, all dated from 2021–2026. There were zero exclusions for year, correction, erratum or review. Forty journals of doubtful quality and 107 records out of scope were set aside. That left 235 eligible and 24 included by manual selection, with priority for meta-analyses, trials or broad-sample designs in compulsory education and for relevance to dosage, mode of delivery, who tutors or scale. Twenty sources have an abstract; four are cited by title only (Dela Cruz et al., 2025; Schult et al., 2026; Zhang et al., 2026; Zhang and Liu, 2022). Zero Latin American studies. Two from low- or middle-income countries: Angrist et al. (2021) and Singh et al. (2026). The cut biases the set towards the United States and Europe. Design inference, on method. A Crossref-only review does not claim that Latin American studies do not exist; it claims that these 16 queries did not recover any of sufficient quality for the 24.

4. What meta-analyses and randomised trials show

Empirical finding. Nickow et al. (2024) meta-analyse tutoring experiments in PreK–12. The pooled effect is 0.288 standard deviations (standard error = 0.029, p < 0.001). Sizes tend to be larger with teacher or paraprofessional tutors, in earlier grades, on at least three days a week and during school. That 0.288 is an average across heterogeneous trials, not the effect to be expected from a national programme in its first year.

Empirical finding. Kraft et al. (2026) extend the meta-analysis to 263 randomised controlled trials. When they better align the sample with large-scale programmes evaluated with independent standardised tests, the pooled effects fall to 0.16 to 0.22 standard deviations, against 0.40 in the full sample, driven by the increase in scale. The authors explore four hypotheses—the abstract does not name them—and document that a package of recommended design features partially protects programmes from that attenuation. To cite only 0.288 or 0.40 in order to justify a mass expansion is to choose the most favourable estimate, not the most pertinent one.

Empirical finding. de Ree et al. (2023) evaluate high-dosage tutoring in three primary schools in a low-income neighbourhood in the Netherlands. After one school year, the effect in mathematics is 0.28 standard deviations of the national population (p < 0.01) and can account for approximately 40% of the mathematics achievement gap between low- and high-income students. Hamlin et al. (2026) evaluate, in a three-year trial, a university-led programme in seven high schools: treatment n = 525 (groups of 2:1 or 3:1) against control n = 438 (remedial course). The treatment showed 0.13 SD (almost half a year of learning). There was no evidence that 2:1 was more effective than 3:1. The programme was delivered at high cost.

Empirical finding. Markovitz et al. (2022) evaluate AmeriCorps volunteers (Minnesota and Wisconsin Reading Corps) who tutor one-to-one students from kindergarten to grade 3 who are at risk, under a response-to-intervention framework. They replicate a trial from four years earlier and evaluate the model in Milwaukee. In kindergarten and grade 1, one semester was enough for significantly higher scores; in grades 2 and 3, the effects appeared after a full year. Kortecamp and Peters (2024) randomly assigned 185 kindergarten and grade 1 students, in 13 classrooms, to one-to-one high-dosage tutoring or to teacher-only instruction. The multilevel analysis indicates that tutored students outperformed untutored students on multiple measures. The abstract does not publish an effect size in standard deviations.

Empirical finding. Seerup et al. (2025) conducted a trial in eight Danish primary schools, with 72 students aged six to seven at risk of reading difficulties. The primary analysis indicates that the treatment improved more than the control in literacy and in executive functions except verbal memory; the differences are not statistically significant. Exploratory analyses indicate positive and significant effects on broader constructs of attention and literacy, and null effects on memory. With n = 72, a primary null does not demonstrate the absence of an effect.

Finseraas et al. (2026), already cited as a low-dosage counter-example, find no significant effects 3.5 to 4.5 years later; the point estimates suggest a fade-out of approximately 47% to 58%. A short-run effect is not a trajectory effect.

Empirical finding. Anger et al. (2026) randomly assigned 839 secondary-school students in Germany to online tutoring for low-achieving students. The intention-to-treat effect on mathematics grades, six months later, was 0.06 standard deviations and not significant. Among those who had not received other tutoring services, the programme improved grades by 0.14. On non-academic trajectories, entry into vocational training eighteen months later was 5 percentage points higher, and 12 points higher among those with no prior tutoring. There is, in the abstract, no effect on employment or on wages.

5. The components of dosage: frequency, group size, scheduling and continuity

Four pieces of dosage recur: frequency, group size, integration into the school day and tutor–student continuity, often measured as lessons completed. Added to them are the gap between planned and delivered dosage, and the role of practice at home.

Empirical finding, on frequency. Kortecamp and Peters (2024) operate two or three times a week. Nickow et al. (2024) find larger effects with at least three days a week. Swanson et al. (2026), in 69 schools (N = 770, kindergarten to grade 5) randomised to tutoring by older peers, by adults or to business as usual in the YMCA, find a modest and educationally meaningful intention-to-treat effect of the adults on sight-word efficiency, and smaller and non-significant effects for cross-age tutoring. Receiving 50 lessons or more (complier average causal effect) produced substantial gains for tutors in passage comprehension and for tutees in word reading and fluency, regardless of tutor type.

Empirical finding, on group size. Robinson et al. (2025) assigned students from kindergarten to grade 2 to virtual tutoring at 1:1, at 2:1 or to control. Virtual tutoring increased early literacy by 0.05 SD for all students and by 0.08 SD when English learners and students with disabilities were excluded. The 1:1 arrangement tended to produce larger gains, especially below the benchmark (0.15 SD). Hamlin et al. (2026) find no evidence that 2:1 is more effective than 3:1 in high school. The corpus does not license “always 1:1”.

Empirical finding, on integration into the school day. Ready et al. (2026) evaluate 12 weeks of virtual literacy tutoring during the school day (grades 1 to 4): an intention-to-treat effect of approximately 0.05 SD; only 20% received the recommended dosage; 10 or more sessions, 0.08 SD; 20 or more, 0.26 SD. Placing tutoring on the timetable does not guarantee the dosage. Finseraas et al. (2026) pull the student out for a fixed time. Nickow et al. (2024) observe larger effects during school. The timetable is a condition of dosage, not a substitute for it.

Empirical finding, on delivered dosage. Shmoys et al. (2026) examine live in-person, live virtual and virtual with artificial intelligence. Dosage rates were quite low in all three implementations. All faced problems of scheduling and of tutor quality; the in-person model, insufficient tutor–teacher communication and filtering of recipients; both virtual models, technology; the model based on artificial intelligence, the absence of meaningful adult–student relationships. Without a protected schedule, planned dosage does not become dosage received.

Empirical finding, on home practice. Bachmann et al. (2026) analyse 656 students in grades 2 and 3 receiving one-to-one high-impact tutoring in 56 high-needs schools. The school dosage of fluency predicted weekly growth in oral reading fluency; reading practice at home did not. Whoever moves dosage from the school timetable to the home is betting against the predictor that does appear here.

ComponentEvidence in the corpusWhat it suggestsWhat it does not license
FrequencyNickow et al. (2024): ≥3 days/week. Kortecamp and Peters (2024): 2–3/week. Swanson et al. (2026): 50+ lessons (compliers).Completed dosage outweighs the nominal offer.A universal threshold of lessons.
Group sizeRobinson et al. (2025): 1:1 > 2:1 in virtual early literacy (0.15 SD below the benchmark). Hamlin et al. (2026): 2:1 ≈ 3:1 in high school.1:1 matters more for struggling beginning readers.That 1:1 is always superior.
SchedulingNickow et al. (2024): larger effects in school. Ready et al. (2026): ITT 0.05 SD; 20% at the recommended dosage. Finseraas et al. (2026): low-dosage pull-out.The timetable is the lever of participation.That “on the timetable” suffices without protecting the schedule.
Delivered dosageShmoys et al. (2026): low rates in all three models. Ready et al. (2026): 20% receive the recommended dosage.The bottleneck is delivery.A universal percentage or a universal cost.
Home practiceBachmann et al. (2026): school dosage predicts; home practice does not.Prioritise the school session.That the home is irrelevant for other outcomes.
Table 2. Components of dosage. “What it suggests” is a design inference; “what it does not license” bounds what the abstracts do not sustain.

6. Virtual delivery and who tutors: teachers, volunteers, peers and machines

Mode of delivery and the profile of who tutors change the cost, the supply of staff and the size of the effect. The corpus does not license a single ranking; it does license refusing to treat them as interchangeable.

Empirical finding, on virtual delivery. Robinson et al. (2025) present, according to the authors, the first trial of virtual tutoring for young children: 0.05 SD (0.08 SD when English learners and students with disabilities are excluded), smaller than those typical of in-person early-literacy programmes. Ready et al. (2026) anchor the virtual mode in the school day: 0.05 SD intention-to-treat and 0.26 SD among those who complete the recommended dosage. Anger et al. (2026) find a non-significant intention-to-treat effect (0.06 SD) and 0.14 SD in the subgroup without prior tutoring. Shmoys et al. (2026) compare in-person, live virtual and virtual with artificial intelligence: all three deliver low dosages. Virtual delivery is neither null nor the automatic equivalent of high-dosage in-person tutoring.

Empirical finding, on who tutors. Nickow et al. (2024) observe larger effects with teachers or paraprofessionals. Markovitz et al. (2022) show that AmeriCorps volunteers, within a response-to-intervention framework, produce replicated effects in early-primary literacy. Hamlin et al. (2026) show that university tutors produce 0.13 SD in high-school mathematics, at high cost. The profile comes packaged with training, materials and dosage.

Peer and cross-age tutoring is another object. Empirical finding. Chang et al. (2025) examine 32 studies and observe a positive effect from small to moderate: 0.34 overall, 0.33 for tutees and 0.39 for tutors, with no significant differences by number of sessions, tutor type, risk or subject area. Hidayat and Saad (2025) meta-analyse 24 papers with 3,311 participants on peer tutoring in STEM: 1.23 on academic achievement (95% confidence interval: 0.75 to 1.70, p < 0.001) and 0.40 on other outcomes (0.20 to 0.59, p < 0.001). The 1.23 is not, without further adjustment, comparable with the 0.288 of Nickow et al. (2024) or with the 0.16–0.22 of Kraft et al. (2026).

Empirical finding. Swanson et al. (2026) contrast adult tutors and older peers who deliver Sound Partners in after-school programmes. The intention-to-treat effect modestly favours adults on sight-word efficiency; the difference between adults and peers is not significant. At a full dosage, tutors and tutees gain regardless of type. Structured lessons can reduce the variability of the tutor; they do not turn any peer into a teacher.

Source limitation and contrast of object. The meta-analysis by Zhang et al. (2026) of intelligent tutoring systems and self-regulation is cited solely for the object of its title. No magnitude, direction or equivalence with human tutoring is asserted. Shmoys et al. (2026) identify, in a low-dosage virtual implementation with artificial intelligence, the absence of a meaningful adult–student relationship as an obstacle; that does not evaluate intelligent tutoring systems as a family.

7. The problem of scale: why effects shrink

The problem of scale is that the object which is scaled is rarely the object which was trialled. Kraft et al. (2026) are the central argument: in moving from the full sample of 263 trials (0.40 SD) to studies with greater equivalence to large programmes evaluated with independent standardised tests, the pooled effect lies between 0.16 and 0.22 SD, driven by the increase in scale. A package of recommended design features—not detailed in the abstract—partially protects against that attenuation. Scaling without protecting the package is an implementation decision, not a statistical law.

The points of loss are observable. Shmoys et al. (2026) identify scheduling, tutor quality, tutor–teacher communication, technology and, in the model with artificial intelligence, the relationship. Ready et al. (2026) show that only 20% receive the recommended dosage (0.05 SD intention-to-treat against 0.26 SD with 20 or more sessions). Swanson et al. (2026) show the same gap between offering the programme and completing 50 lessons or more. Scale multiplies those gaps.

Cost is the other limit, and the corpus barely quantifies it. Hamlin et al. (2026) report that a university-led programme with an effect of 0.13 SD was delivered at high cost. They publish no figure per student. Chang et al. (2025) value cross-age tutoring, among other reasons, for its economic advantages; that valuation is the authors’, not a comparative cost.

Finseraas et al. (2026) recall that, with low dosage and the full population, the trace at 3.5–4.5 years is not significant and the point estimates suggest a fade-out of around half. Singh et al. (2026) show that a government out-of-school remediation programme contributed approximately 24% of cohort recovery within six months. To attribute the whole of post-pandemic recovery to tutoring is to ignore the rest of that cohort recovery and the two thirds associated with the return to school.

LinkWhat is lostAnchor
Planned dosageSchedule, a larger group, a tutor who rotates.Nickow et al. (2024); Shmoys et al. (2026).
Delivered dosageLow participation, technology, tutor–teacher communication.Shmoys et al. (2026); Ready et al. (2026): 20%; Swanson et al. (2026): 50+ lessons.
Effect in the trialITT dilutes the compliers; the measure may be proximal to the programme.Ready et al. (2026): 0.05 ITT vs 0.26 with 20+ sessions. Swanson et al. (2026). Anger et al. (2026): ITT 0.06 n.s.
Effect at scaleThe inferential target changes; scale is associated with smaller effects.Kraft et al. (2026): 0.16–0.22 SD vs 0.40 in the full sample.
Figure 1. Conceptual scheme, not a fabricated datum: the chain of loss between planned dosage and the effect at scale (Kraft et al., 2026; Shmoys et al., 2026; Ready et al., 2026; Swanson et al., 2026; Nickow et al., 2024; Anger et al., 2026). The links are not coefficients and are not an estimate of our own.

8. Latin America and Mexico: absent evidence and cautious transfer

The corpus contains no Latin American studies: 0 of 24. The 16 Crossref queries did not recover, at sufficient editorial quality, broad-sample trials or syntheses on high-dosage tutoring or on learning loss and recovery conducted in Latin America or in Mexico. That absence is a limitation of this review, not proof that the region has produced no research. Stating it prevents the 0.288 of Nickow et al. (2024) or the 0.40 of Kraft et al. (2026) from being imported as national parameters.

The evidence from low- or middle-income countries comes from two sources. Angrist et al. (2021) estimate, in five African countries, a loss of half a year to more than one year, and model 2.8 years by grade 10 from a deficit in grade 3; they propose targeted instruction and structured pedagogy. Singh et al. (2026) document, in rural Tamil Nadu, a large and regressive loss, a rapid and progressive recovery, and a contribution of approximately one quarter from a government out-of-school programme. Neither source is a map of Mexico.

What follows is a design inference, not a Mexican empirical finding: it describes neither existing programmes nor national figures.

Design inference, for Mexico. First: a design that leaves dosage to the afternoon, the weekend or a home platform chooses the most fragile link (Nickow et al., 2024; Ready et al., 2026; Shmoys et al., 2026). Second: the Consejo Técnico Escolar is a natural candidate for the tutor–teacher communication that Shmoys et al. (2026) identify as a failure of the in-person model; this is not an evaluation of technical councils. Third: student teachers on practicum (normalistas) or students on social-service placements, with training and structured materials, are the local analogue of teachers, paraprofessionals, volunteers working within a framework and university students (Nickow et al., 2024; Markovitz et al., 2022; Hamlin et al., 2026); they are not, merely by existing, high-dosage tutors. Fourth: prioritising early primary grades in reading and mathematics is consistent with the corpus and is not universal coverage (Nickow et al., 2024; Kortecamp and Peters, 2024; Markovitz et al., 2022; Robinson et al., 2025; Seerup et al., 2025; de Ree et al., 2023; Wisenöcker et al., 2025). Fifth: a system that does not measure sessions received, continuity of the tutor and the actual size of the group evaluates the organisational chart, not the programme (Ready et al., 2026; Swanson et al., 2026; Shmoys et al., 2026).

9. Design implications for schools and systems

The rules that follow are a design inference drawn from the corpus, not a new causal finding and not a cost-effectiveness calculation.

  1. Protect dosage inside the school timetable. A programme that exists in the annual plan and not in the weekly timetable is not high-dosage tutoring (Nickow et al., 2024; Ready et al., 2026; Shmoys et al., 2026).
  2. Keep groups small and stable, of one to three or four, without assuming that 1:1 is always superior. Size is chosen with the grade, the subject and the cost (Robinson et al., 2025; Hamlin et al., 2026).
  3. Look after continuity of the tutor. Rotating tutors in order to fill gaps dilutes the dosage without changing the name of the programme (Nickow et al., 2024; Kortecamp and Peters, 2024; Shmoys et al., 2026).
  4. Use structured materials aligned with a sequence of skills. The material does not replace the tutor; it reduces improvisation when the tutor is not an expert teacher (Kortecamp and Peters, 2024; Swanson et al., 2026; Angrist et al., 2021).
  5. Monitor the dosage delivered, not only the dosage enrolled. The operational indicator is sessions received per student, with the same tutor, at the planned group size (Swanson et al., 2026; Ready et al., 2026; Shmoys et al., 2026).
  6. Evaluate with tests that are independent of the tutor’s materials when the policy target is general achievement (Kraft et al., 2026).
  7. Set realistic expectations for the effect at scale. The order of magnitude of actual operation is closer to 0.16–0.22 SD, 0.13 SD or 0.05 SD intention-to-treat than to 0.288 or 0.40 (Kraft et al., 2026; Hamlin et al., 2026; Robinson et al., 2025; Ready et al., 2026; Nickow et al., 2024).
  8. Plan for persistence, not only for the semester of launch. A programme that is switched off when “normality” returns is betting that the effect of one year will be conserved on its own; the corpus does not guarantee that conservation (Finseraas et al., 2026; Anger et al., 2026).

The policy question is one of allocation: who is prioritised, with which tutor, at what cost, and with what threshold of delivered dosage the design is revised. The corpus does not answer it for Mexico; it does rule out a generic yes or a generic no.

10. Limitations

The base is exclusively Crossref. ERIC, PsycINFO, SciELO and Redalyc were not searched. The 16 queries and the lexical screening in screen.py are reproducible; the final selection of 24 sources is manual and is not double-coded. Four sources are cited by title only. The geographical predominance is that of the United States and Europe. There are zero Latin American studies. There are two from low- or middle-income countries (Angrist et al., 2021; Singh et al., 2026), and neither is a trial of high-dosage tutoring. Transfer to Mexico is an inference, not a datum.

The measures are heterogeneous: tests proximal to the programme, nationally recognised tests, course grades, oral reading fluency, executive functions and entry into vocational training. To average them in prose would be an informal meta-analysis. Several trials have small samples—Seerup et al. (2025) with 72 students; Kortecamp and Peters (2024) with 185 in 13 classrooms—and, as an inference of this review, small trials with large effects may be over-represented because of publication bias; the drop in effects when sample and scale are aligned, which Kraft et al. (2026) document, is compatible with that risk, although their abstract does not attribute it to that cause. Cost appears as a qualitative statement (Hamlin et al., 2026). None of the foregoing licenses either inflating or cancelling the published signs.

11. Conclusions

High-dosage tutoring is a policy of dosage, not a recovery label. Nickow et al. (2024) document a pooled effect of 0.288 SD in field trials, larger with teachers or paraprofessionals, in the early grades, on at least three days a week and during school. That result sustains the claim that the package exists; it does not sustain the claim that a system which enters “tutoring” in its plan will observe 0.288 SD on a national test.

Kraft et al. (2026) find 0.16 to 0.22 SD when the sample is aligned with large programmes and independent tests, against 0.40 in the full sample. Shmoys et al. (2026), Ready et al. (2026) and Swanson et al. (2026) show the mechanism: delivered dosage falls short of planned dosage. Hamlin et al. (2026) add that 0.13 SD in high school can be both significant and expensive. Finseraas et al. (2026) recall that a lower-dosage intervention may leave no trace years later.

Who tutors, and in which mode, is not a logistical detail. Teachers and paraprofessionals concentrate the largest effects (Nickow et al., 2024); volunteers working within a structured framework produce replicated effects (Markovitz et al., 2022); university tutors produce effects at high cost (Hamlin et al., 2026); peers yield evidence from small to moderate and, in STEM, of a larger magnitude that is not comparable (Chang et al., 2025; Swanson et al., 2026; Hidayat and Saad, 2025). Virtual delivery works, with smaller effects, for beginning readers and depends on the dosage completed (Robinson et al., 2025; Ready et al., 2026). Intelligent tutoring systems are a different object, not a demonstrated substitute.

Latin America and Mexico are not in the evidence included. Angrist et al. (2021) and Singh et al. (2026) document loss and recovery in Africa and in India. Transferring the package to Mexico is an inference: a protected timetable, tutor–teacher coordination, trained tutors—including normalistas or university social service—priority for early-primary reading and mathematics, and measurement of the dosage delivered.

The question that remains is not whether tutoring “works”. It is what dosage is delivered, within the timetable, by whom, for whom priority is set and at what cost, and with which test success is declared.

NEXTECH.IA Editorial Lab / Ingeniero Mitre

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