A trial reports:
Overall impact: +1 month.
Then the subgroup table shows:
Pupils eligible for Free School Meals: +2 months.
The temptation is immediate.
“The programme works twice as well for disadvantaged pupils.”
That conclusion may be true.
The table alone does not establish it.
Subgroup results are among the easiest education statistics to overread because the human mind is built to notice differences. We see +2 and +1 and assume the gap itself is evidence.
But research asks a harder question:
Is there credible evidence that the treatment effect actually differs between the groups, rather than the displayed estimates being separated by sampling noise?
That requires more than looking at two numbers.
It requires thinking about:
- subgroup sample size;
- uncertainty;
- whether the subgroup was prespecified;
- whether the analysis tested an interaction;
- how many subgroups were examined;
- whether the subgroup definition is meaningful;
- whether the mechanism makes sense;
- whether the pattern replicates;
- whether implementation differed;
- whether the outcome is comparable.
This article owns that interpretation mechanism.
It does not own causal inference in general, statistical power in general, research bias, equity strategy or intervention design. It asks a narrower question:
When an education trial reports different effects for different groups, how should a careful reader decide whether the apparent difference is informative, exploratory or misleading?
The central mechanism is:
subgroup estimate → uncertainty → formal difference test → prespecification → multiplicity → mechanism → replication → decision
The first number is easy.
The reasoning begins after it, because subgroup evidence is useful only when the difference itself has earned the right to influence interpretation, targeting or education policy decisions responsibly.
The 50-second route
If you only have a minute, keep this:
- A subgroup effect is the estimated treatment effect within a defined subset of the sample.
- A larger subgroup estimate does not automatically prove the programme works better for that group.
- “Significant in Group A, not significant in Group B” is not the same as “the effect differs significantly between A and B”.
- The stronger question is usually an interaction: is the difference between subgroup effects larger than we would expect from sampling variation?
- Subgroups have fewer participants, so their estimates are usually less precise.
- Prespecified subgroups are more credible for confirmatory claims than groups discovered after seeing the data.
- Testing many subgroups increases the chance of finding an eye-catching pattern by chance.
- Subgroup definitions should have educational meaning; arbitrary splits can manufacture unstable differences.
- A demographic label is not itself a mechanism. Ask what feature of context, implementation, baseline knowledge or access could produce differential impact.
- Replication matters. One striking subgroup result should usually update a hypothesis, not settle it.
- Use subgroup evidence to ask better implementation and equity questions—not to build permanent labels around pupils.
- The shortest rule is: a difference between numbers is not automatically evidence of a difference between effects.
1. What is a subgroup effect?
Suppose a randomised trial includes 4,000 pupils.
Researchers estimate the average treatment effect across everyone.
Then they examine:
- pupils eligible for Free School Meals;
- pupils not eligible;
- girls;
- boys;
- pupils with lower prior attainment;
- pupils with higher prior attainment.
Each subgroup can have its own estimated intervention–comparison difference.
Those estimates can be useful.
They can also be much noisier than the overall result because each uses fewer observations.
The subgroup table is a zoom lens.
Zoom reveals structure.
It also magnifies noise.
2. The average can hide real variation
Average effects matter.
They answer: “What happened across the study population, on average?”
But an average can combine different responses.
Imagine:
Group A effect = +0.40.
Group B effect = 0.00.
Overall effect = +0.20.
If the difference is real, the average conceals an important pattern.
This is why researchers care about heterogeneous treatment effects.
Education interventions may interact with:
- prior attainment;
- age;
- language;
- disability;
- socioeconomic conditions;
- school context;
- implementation dose;
- baseline risk.
Subgroup analysis can reveal where an intervention appears especially promising or ineffective.
The challenge is separating true heterogeneity from random fluctuation.
3. Every subgroup estimate carries uncertainty
Suppose:
Overall: effect size 0.10, based on 5,000 pupils.
FSM subgroup: effect size 0.18, based on 1,000 pupils.
Non-FSM subgroup: effect size 0.08, based on 4,000 pupils.
The FSM estimate is larger.
It is also based on fewer pupils.
Its confidence interval will often be wider.
The visible point estimate is only the centre of an uncertainty range.
A subgroup result should be read with that uncertainty attached.
4. Smaller samples make striking estimates more common
Sampling variation is more volatile in small groups.
This can produce:
- unusually large positive effects;
- unusually negative effects;
- apparent reversals;
- instability across replications.
This is not because subgroup analysis is bad.
It is because precision depends partly on information quantity.
When a report itself says a subgroup finding is less secure because of smaller sample size, that is not a footnote to ignore.
It is part of the result.
5. The classic mistake: significant here, not significant there
Researchers analyse:
Group A: effect significant.
Group B: effect not significant.
Headline: “Programme works for Group A but not Group B.”
This can be statistically wrong.
Why?
Because significance within each group depends on both estimate and precision.
Two similar effects can produce different significance labels if one subgroup is larger.
Example:
Group A: effect 0.20, narrow interval → significant.
Group B: effect 0.18, wide interval → not significant.
The effects are almost the same.
The evidence strength differs.
To claim the effects differ, test the difference between effects.
6. Interaction is the central idea
An interaction asks:
Does the intervention effect change as a function of subgroup membership?
Conceptually:
[(Intervention – Control)_{Group A} – (Intervention – Control)_{Group B}]
Is that difference credibly different from zero?
This is the statistical question behind:
“Does the programme work differently for these groups?”
The exact model depends on design.
The conceptual discipline is universal.
Do not infer interaction from two point estimates by eye.
7. Current EEF evidence gives a clean example
EEF’s Stop and Think page reports:
science overall: about +2 months.
FSM pupils: about +1 month.
Then EEF says there is not evidence to suggest pupils are differently impacted by the programme.
This is exactly the distinction.
The point estimates differ numerically.
The evidence does not support a confident differential-impact claim.
A careful reader should learn from the wording, not just the table.
8. Another current example: Mathematical Reasoning
EEF’s 16 September 2026 release reports:
Year 2 pupils overall: approximately +1 month in Mathematics.
FSM-eligible pupils: approximately +2 months.
This is encouraging.
But the subgroup estimate should not be converted instantly into:
“the programme doubles its effect for disadvantaged pupils.”
The next questions are:
- How large is the FSM sample?
- How precise is the estimate?
- Was the subgroup prespecified?
- Was an interaction tested?
- Does the evaluation report support a differential-impact claim?
- Does the pattern replicate?
A larger point estimate is a signal.
It is not the whole inference.
9. Current example: Focus4TAPS second trial
EEF’s second Focus4TAPS trial reports:
overall science: 0 months, effect size about 0.03.
FSM pupils: +1 month, effect size about 0.07.
EEF explicitly advises that the FSM result should be interpreted more cautiously because the subgroup is smaller.
This is excellent statistical communication.
The subgroup estimate can still matter.
But uncertainty should travel with it.
10. Current example: Peep-LTS
EEF’s Peep Learning Together Programme reports exploratory subgroup findings for children eligible for Early Years Pupil Premium.
The page notes positive subgroup estimates, including around +4 months for some outcomes.
It also explicitly warns that the subgroup samples were small and the effects have lower security than the overall findings.
The correct response is neither: “ignore the subgroup” nor “programme definitely works especially for EYPP pupils”.
The correct response is: “promising exploratory signal; uncertainty high; seek replication and mechanism.”
11. Prespecification protects credibility
Before researchers see results, they can specify:
“We will examine whether impact differs by FSM eligibility.”
This is stronger than:
“After seeing the data, we tried twenty pupil characteristics and found one striking difference.”
Why?
Because if enough subgroups are searched, chance patterns become likely.
Prespecification makes the analytic intention visible before the result can influence the choice.
It does not guarantee the subgroup claim is true.
It improves interpretive credibility.
12. IES guidance supports limited, meaningful subgroup analysis
Current Institute of Education Sciences guidance for rigorous education studies emphasises defining meaningful subgroups in advance where confirmatory claims are intended, limiting the number of subgroup tests, specifying definitions clearly and providing an a priori rationale.
The logic is straightforward.
A subgroup should exist because there is a defensible educational reason to expect impact variation, not merely because the variable is available in the dataset.
13. Multiple testing creates false discovery pressure
Suppose researchers test effects by:
- sex;
- FSM;
- ethnicity;
- prior attainment;
- language;
- SEND;
- urban/rural;
- school size;
- teacher experience;
- baseline motivation.
Then split each again.
Many comparisons.
Even if the intervention effect is truly constant, some subgroup differences may look unusual by chance.
This is the multiple-comparisons problem.
The more fishing, the more likely something shines.
14. Correction methods help, but interpretation still matters
Statistical procedures can adjust for multiple testing.
But no correction substitutes for:
- a good prior hypothesis;
- meaningful subgroup definition;
- adequate sample;
- plausible mechanism;
- replication.
A corrected nonsense subgroup remains nonsense.
Statistics cannot supply educational meaning after the fact.
15. Exploratory subgroup analysis still has value
Exploratory does not mean worthless.
It means:
“Use this to generate or update hypotheses, not to make the strongest confirmatory claim.”
An unexpected pattern can guide:
- next trial;
- implementation research;
- qualitative inquiry;
- targeted measurement.
Science often advances by noticing anomalies.
The discipline is labelling the strength of evidence honestly.
16. Subgroup definitions can be arbitrary
Researchers sometimes split a continuous variable:
“low prior attainment” vs “high prior attainment”.
Where is the cut?
Median? Quartile? Policy threshold?
Different cut-points can change results.
Dichotomising continuous variables also throws away information.
Where appropriate, modelling a continuous moderator can be more informative than forcing pupils into two boxes.
The subgroup definition is part of the claim.
17. Policy categories can still be useful
FSM eligibility, SEND status and language categories can be administratively meaningful and important for equity analysis.
But policy usefulness does not make them causal mechanisms.
“FSM pupil” is not one psychological trait.
The category may correlate with:
- material resources;
- school access;
- prior learning;
- neighbourhood;
- tutoring;
- attendance;
- stress;
- many other factors.
If effects differ, ask what process might explain the difference.
18. Demographic labels are not mechanisms
Weak interpretation:
“Girls respond better to this programme.”
Stronger:
“In this trial, the estimated effect was larger for girls. Possible explanations might involve baseline differences, implementation, participation patterns or chance; the analysis should test and replicate the differential effect.”
Demographics describe groups.
Mechanisms explain why effects differ.
Do not stop at the label.
19. Baseline room-to-grow can matter
Suppose lower-attaining pupils begin far below the test ceiling.
Higher-attaining pupils begin near it.
A programme may appear to have larger effects for the lower group partly because the measure offers more room to change.
Or the reverse can happen if the task is too difficult for lower-attaining pupils.
Subgroup interpretation should inspect floor and ceiling effects.
Measurement conditions can mimic treatment heterogeneity.
20. Outcome choice can change subgroup patterns
A programme may show:
- similar effects across groups on a broad test;
- larger effects for one group on an aligned measure.
Which is the “real” subgroup effect?
Both are results on different constructs or sensitivity levels.
The mechanism claim requires outcome interpretation.
Do not generalise “works better for Group A” without naming the outcome.
21. Implementation can differ by subgroup
Perhaps one group attends more sessions.
Perhaps teachers adapt materials differently.
Perhaps baseline accessibility differs.
If impact varies, implementation variation may be part of the explanation.
Subgroup analysis should connect to process data where possible.
The treatment received may not be uniform even when assignment was random.
22. School-level context can create apparent pupil subgroup effects
Suppose FSM pupils are concentrated in certain schools.
Those schools also implement the programme differently.
A simple pupil subgroup difference may partly reflect school context.
Multilevel education data complicates subgroup inference.
Researchers need models that respect the design and clustering.
Practitioners do not need to run the model.
They do need to avoid simplistic causal stories.
23. Intersectional subgroups become small quickly
FSM + multilingual + SEND + one ethnic group + low prior attainment.
The category may be educationally meaningful.
The sample may contain very few pupils.
Precision collapses.
This is a real tension in equity research:
the groups we most want to understand may be statistically hardest to estimate precisely.
The answer is not to ignore them.
It is to collect enough data, combine evidence carefully and communicate uncertainty.
24. Power for overall effects is not power for interaction effects
A trial can be large enough to detect the overall average effect and still be underpowered to detect treatment-effect differences between subgroups.
Interactions often require substantial sample size.
This is why “we found no subgroup difference” can sometimes mean:
“the study was not precise enough to rule out meaningful differences.”
Absence of evidence is not always evidence of equal effects.
25. IES methodological work is actively addressing heterogeneity
An IES-funded methodological project on impact variation in randomised trials explicitly focuses on the interest in subgroup effects and whether effects differ, including machine-learning methods that can explore heterogeneous impacts without requiring all subgroups to be specified in advance.
This is an active research frontier.
Machine learning can discover patterns.
It also raises new validation questions.
Discovery still needs out-of-sample testing, interpretation and replication.
26. Data-driven subgroup discovery can overfit
A flexible algorithm can find complex patterns in one dataset.
Those patterns may not survive a new sample.
The more flexible the discovery system, the more important:
- cross-validation;
- holdout data;
- replication;
- mechanism plausibility.
A subgroup should not become a policy category because one model split the data there once.
27. Relative and absolute effects can differ
Suppose an intervention improves test scores by a similar standardised amount across two groups.
But one group starts at much higher baseline risk of failure.
The absolute policy consequence may differ.
Alternatively, a small relative effect can translate into many pupils crossing a threshold in one group.
Subgroup decisions may need both:
- relative treatment effect;
- absolute outcome level.
One metric rarely answers every equity question.
28. Subgroup analysis can reveal harm
Most attention goes to “who benefits more?”
But the more important question can be: “Is any group harmed?”
A positive overall average can conceal negative impact for a subgroup.
If the evidence is credible, this matters ethically and practically.
Safety monitoring is a form of heterogeneity analysis.
Again, small groups require careful interpretation rather than dismissal.
29. A subgroup result should change action in proportion to evidence
Weak exploratory signal: investigate further.
Moderate credible signal: monitor implementation and outcomes for that group.
Strong replicated differential effect with mechanism: consider targeted adaptation or eligibility.
Do not jump from a single subgroup table to permanent programme exclusion or targeting.
Evidence strength should control decision strength.
30. Subgroup findings can improve implementation without restricting access
Suppose lower-attaining pupils benefit less.
The response need not be: “do not give them the programme.”
Ask:
- do they need prerequisite teaching?
- is task language too demanding?
- is dose lower?
- does the support require adaptation?
Heterogeneity can reveal a design problem rather than a fixed learner limitation.
31. The fairness danger: turning averages into identities
“FSM pupils respond better.”
Soon: “This is the FSM intervention.”
That can create:
- stigma;
- reduced choice;
- incorrect targeting;
- neglect of eligible individuals outside the category.
Subgroup evidence should inform systems cautiously.
It should not become destiny.
32. The opposite fairness danger: refusing subgroup analysis
“We treat everyone the same, so only the overall effect matters.”
That can conceal unequal impact.
Equity requires enough disaggregation to notice:
- benefit gaps;
- access gaps;
- harms;
- implementation differences.
The solution is rigorous subgroup analysis, not no subgroup analysis.
33. Worked example: significant/not-significant fallacy
Group A: effect = 0.20, p = .03.
Group B: effect = 0.16, p = .11.
Bad conclusion: “Works for A but not B.”
The estimates are close.
The difference between 0.20 and 0.16 may be tiny relative to uncertainty.
Need: formal interaction/difference test.
The p-values within groups answer separate questions.
34. Worked example: numerically different, interaction weak
Group A: +0.30.
Group B: +0.10.
Looks large.
But: A has 80 pupils. B has 90. Intervals are wide.
Interaction estimate: 0.20 with uncertainty spanning substantial negative and positive values.
Interpretation: possible heterogeneity, not established.
The eye sees a difference faster than the study can support it.
35. Worked example: small difference, strong evidence
Group A: +0.18.
Group B: +0.12.
Difference only 0.06.
But in a huge study the interaction may be estimated precisely.
Statistical evidence can support a small differential effect.
Whether 0.06 is educationally meaningful is a second question.
Statistical and practical significance are different.
36. Prespecification is not prophecy
Researchers can prespecify a subgroup and still find nothing.
They can prespecify the wrong mechanism.
They can define the group poorly.
Prespecification improves credibility by reducing data-driven selection.
It does not make the hypothesis correct.
37. Replication is the strongest antidote to subgroup excitement
A pattern appears once.
Ask: Does it recur?
Same programme, new schools. Same subgroup definition. Same outcome. Similar direction. Similar implementation.
Replication can convert an exploratory pattern into stronger evidence.
Non-replication is also information.
38. Meta-analysis can examine effect moderators—but with caveats
Across studies, researchers may ask whether effects vary by:
- age;
- dosage;
- subject;
- implementation;
- participant characteristics.
Moderator analysis can reveal systematic heterogeneity.
But study-level moderators can be confounded.
A programme delivered to older students may also use different materials.
Meta-regression does not magically recreate randomisation across study characteristics.
Interpret mechanisms carefully.
39. EEF’s language around subgroup findings is a useful model
Strong evidence communication often uses phrases such as:
- “should be interpreted more cautiously”;
- “exploratory subgroup analysis”;
- “smaller sample size”;
- “no evidence to suggest pupils are differently impacted”.
These phrases are not hedging to be edited out of the headline.
They are part of the statistical result.
Schools should preserve them when communicating.
40. Parents: how to read “works better for disadvantaged pupils”
Ask:
- Was the subgroup analysis planned?
- How many pupils were in it?
- Was the difference between groups formally tested?
- How wide is the uncertainty?
- Does the report call it exploratory?
- Is there a plausible mechanism?
- Has the pattern replicated?
Do not assume the category predicts your individual child.
41. Teachers: how to read subgroup tables
Use the subgroup result as a prompt.
If one group appears to benefit less:
- inspect participation;
- inspect access;
- inspect baseline prerequisites;
- inspect dose;
- inspect classroom adaptation.
Do not lower expectations or remove opportunity based on one uncertain table.
42. School leaders: distinguish targeting evidence from targeting enthusiasm
A subgroup result can tempt leaders:
“Buy this for Group X.”
Before targeting, require:
- credible differential effect;
- relevant local population;
- plausible mechanism;
- practical fit;
- monitoring plan;
- consideration of pupils outside the subgroup who may also benefit.
Targeting is a stronger decision than interpretation.
It deserves stronger evidence.
43. Researchers: report the denominator
Subgroup results should make sample size visible.
“+3 months for subgroup X” is incomplete without a sense of how many pupils contributed and how precise the estimate is.
Readers need to understand that a dramatic effect from a tiny sample is not equivalent to the same point estimate from thousands.
44. Researchers: report the interaction, not only separate p-values
If the claim is differential impact, show the statistical test supporting differential impact.
This should become normal evidence literacy.
Practitioners do not need to calculate interactions.
They need to know whether the report actually tested the claim being communicated.
45. Researchers: say whether analysis was confirmatory or exploratory
This one label improves interpretation enormously.
Confirmatory: prespecified hypothesis, analysis planned before outcome inspection.
Exploratory: pattern investigated after or beyond primary plan.
Both can be valuable.
They support different claim strengths.
46. Common failure mode: subgroup shopping
Analysts test many categories and report only the dramatic one.
Repair: prespecify, disclose full analysis set, correct or contextualise multiplicity.
47. Common failure mode: significance split
A significant result in one group and nonsignificant in another is declared differential.
Repair: test the interaction.
48. Common failure mode: point estimates without uncertainty
Repair: read confidence intervals, sample sizes and report caveats.
49. Common failure mode: demographic label becomes causal story
Repair: seek mechanism and implementation evidence.
50. Common failure mode: tiny subgroup, huge headline
Repair: treat as exploratory unless supported by strong precision/replication.
51. Common failure mode: no subgroup analysis because overall effect is positive
Repair: check for plausible equity-relevant heterogeneity and harm.
52. Common failure mode: one subgroup result dictates eligibility
Repair: match decision strength to evidence strength.
53. Common failure mode: arbitrary split
Repair: justify thresholds or use continuous moderation where appropriate.
54. Common failure mode: multiple outcomes ignored
Programme “works better for Group A” on one outcome, not others.
Repair: name the outcome and consider coherence across measures.
55. Common failure mode: implementation differences ignored
Repair: connect subgroup results to dose, attendance, teacher practice and access.
56. A subgroup-effect reading protocol
When you see a subgroup table, record:
Overall effect: ______
Subgroup effect A: ______
Subgroup effect B: ______
Subgroup N: ______
Confidence/uncertainty: ______
Prespecified? ______
Interaction tested? ______
Multiplicity handled? ______
Outcome: ______
Plausible mechanism: ______
Implementation differences: ______
Replication: ______
Decision warranted: ______
This turns an attractive table into an evidence question.
57. The learner route: a research-literacy habit
If an article says:
“The programme worked for boys but not girls,”
ask:
“Did the study test whether the effects differed, or did it only report significance separately?”
That one question protects against a very common inference error.
58. The teacher route: use subgroup evidence to generate observations
Suppose a report suggests lower impact for pupils with weaker prior attainment.
In your classroom, monitor:
- entry prerequisites;
- time on task;
- misunderstanding;
- need for scaffolding;
- completion;
- feedback uptake.
Use the subgroup result to sharpen observation.
Do not convert it into a label.
59. The school route: build equity monitoring into implementation
If a programme is adopted, collect appropriate outcome and implementation data by relevant groups where ethical and feasible.
Ask:
- who receives the intended dose?
- who drops out?
- who can access materials?
- who benefits?
- who experiences burden?
Local monitoring cannot reproduce a randomised trial.
It can reveal implementation inequity early.
60. Machine learning does not remove the need for theory
Modern methods can discover complex heterogeneity.
That is powerful.
But a model saying: “these characteristics predict larger treatment effects” does not automatically explain why.
Policy needs interpretation.
The strongest workflow is:
discovery → validation → mechanism → replication → decision.
Not: discovery → permanent label.
61. How subgroup evidence matures
Think in levels:
Level 1: numerical pattern
Point estimates differ.
Level 2: statistical evidence
Interaction/differential effect supported.
Level 3: prespecified/robust evidence
Pattern survives appropriate inferential controls.
Level 4: mechanism evidence
We understand a plausible causal pathway.
Level 5: replication
Pattern recurs in new data/settings.
Level 6: actionable targeting
Evidence supports a practical differential decision.
Most subgroup findings should not jump directly from Level 1 to Level 6.
Frequently asked questions
What is a subgroup effect?
The estimated treatment effect within a defined subset of participants, such as pupils eligible for Free School Meals or pupils with lower prior attainment.
If one subgroup has +2 months and another +1, does the programme work better for the first?
Not necessarily. The difference may reflect sampling uncertainty. Look for an interaction/differential-effect test.
What is an interaction?
A test of whether the intervention effect changes depending on subgroup membership or another moderator.
Why are subgroup findings often less secure?
Subgroups have fewer participants, producing less precise estimates. Multiple testing and post-hoc selection can add uncertainty.
Is exploratory subgroup analysis bad?
No. It is useful for generating hypotheses and identifying possible heterogeneity. It should be labelled and interpreted more cautiously than prespecified confirmatory analysis.
Why prespecify subgroups?
It reduces the risk of selecting interesting-looking groups only after seeing results and clarifies the original hypothesis.
Can a nonsignificant subgroup effect still be important?
Yes. It may be imprecisely estimated. Consider the point estimate, interval, sample and interaction rather than significance label alone.
Should schools target programmes using subgroup results?
Only when the differential evidence is sufficiently credible, relevant and actionable. One exploratory subgroup finding is rarely enough.
Can subgroup analysis improve equity?
Yes. It can reveal unequal benefit, access or harm. But careless subgroup claims can also stigmatise or mis-target learners.
What is the strongest practical rule?
Do not confuse a visible difference between subgroup estimates with evidence that treatment effects truly differ.
The deeper lesson: fairness requires disaggregation, and fairness also requires restraint
Education should care about averages.
A programme that raises attainment across thousands of pupils matters.
Education should also care about who benefits.
An average can hide pupils for whom the programme is less accessible, less effective or actively harmful.
That is why subgroup analysis matters.
But the ethical importance of the question does not make the statistics easier.
Smaller samples are noisy. Labels are imperfect. Many comparisons generate chance patterns. Demographic categories can be mistaken for mechanisms. A promising signal can become a policy stereotype before it is replicated.
So the mature position is neither:
“ignore subgroups because averages are cleaner”
nor:
“believe every subgroup difference because equity matters.”
It is:
look carefully, test the difference, preserve uncertainty, seek mechanism, replicate, and make decisions no stronger than the evidence.
Subgroup analysis works when it helps education see variation without turning variation into destiny. The statistical task is to discover whether variation is credible; the educational task is to decide whether that variation reveals a mechanism, an implementation problem, an equity concern or simply uncertainty that the next study must resolve.
Sources
- Institute of Education Sciences, Investigating the Potential of Machine Learning Methods for Identifying Impact Variation in Randomized Control Trials: https://ies.ed.gov/use-work/awards/investigating-potential-machine-learning-methods-identifying-impact-variation-randomized-control
- Institute of Education Sciences, Standards for Excellence in Education Research / subgroup analysis guidance: https://ies.ed.gov/
- Education Endowment Foundation, Mathematical Reasoning trial press release (16 September 2026): https://educationendowmentfoundation.org.uk/news/trial-finds-teaching-reason-about-maths-boosts-attainment
- Education Endowment Foundation, Focus4TAPS — second trial: https://educationendowmentfoundation.org.uk/projects-and-evaluation/projects/focus4taps-2024-25-trial
- Education Endowment Foundation, Peep Learning Together Programme: https://educationendowmentfoundation.org.uk/projects-and-evaluation/projects/peep-learning-together-programme
- Education Endowment Foundation, Stop and Think: https://educationendowmentfoundation.org.uk/projects-and-evaluation/promising-programmes/stop-and-think