What the 2026 Teacher EQ Training Review Adds

What does the July review add that a broad EI review cannot?

The July 2026 review, “Emotional intelligence training programs for teachers: a systematic review,” narrows the question to a particular kind of work: teaching, where emotional decisions recur in interactions with students, families, colleagues, and school leaders. It included 27 quantitative intervention studies of school teachers and preservice teachers. Each measured emotional intelligence before and after training; eligible programs had to target EI directly and assess it with a validated instrument. Broader social-emotional learning programs qualified only when they explicitly measured EI, while studies of other human-service professionals did not. The review offers a profession-specific map of what was taught, measured, and reported, rather than a general answer about every workplace. Its four-database search covered Scopus, Web of Science, ERIC, and PsycINFO, from February through October 2023. Although published on 2 July 2026, its evidence search did not reach studies after that cutoff. The publication date is not an evidence-through-July date. A separate 2025 review, “The effects of emotional intelligence training programs on educators: a systematic review,” maps a broader set of educator publications; its scope differs, so its larger publication count cannot be read as a comparable effectiveness sample. The July review adds a clearer view of teacher-specific evidence and its boundaries. Later teacher studies and broader workplace findings still need separate consideration.

Sources: Emotional intelligence training programs for teachers: a systematic review; The effects of emotional intelligence training programs on educators: a systematic review

What does the 25-of-27 result actually say?

Twenty-five of the 27 studies in “Emotional intelligence training programs for teachers: a systematic review” reported a statistically significant improvement in at least one measured emotional-intelligence (EI) dimension. The result is a count of studies with a favorable finding somewhere among their measured outcomes. It does not tell us the typical size of a change, whether every dimension improved, or whether the change would be visible in how colleagues work together. The review itself reports that results varied across studies and measures. The distinction matters because statistical significance answers a narrower question than practical importance. A significant result indicates that a study’s data met its chosen statistical threshold for a change; it does not say whether that change was large enough to matter in a classroom, durable after a course, or relevant to a workplace interaction. The review does not pool a common effect size for the 25 studies. Its 25-of-27 headline therefore cannot be read as “most participants improved by a meaningful amount” or as an estimate of what a new training program should achieve. The review required each included study to measure EI before and after training, so all 27 had a pretest–posttest comparison. Twenty also included a control group; seven did not. A control group helps distinguish a change during training from changes that might have occurred over the same period without it. But those 20 comparisons were not all randomized: only seven studies used some form of randomization. The count of significant findings consequently combines evidence from different designs, with different strength for attributing change to the intervention. A before-and-after result without a comparison group can show that scores changed; by itself, it cannot show that training caused the change. There is another reason not to treat the count as a direct verdict. The studies assessed multiple EI dimensions, and the review records whether each study found a significant gain in at least one. That rule gives a study credit for a finding on one dimension even if other measured dimensions did not improve. The review’s detailed results show this pattern: some studies reported gains across all assessed dimensions, while others reported gains in only some, and four trait or mixed-model studies reported no significant change across their assessed dimensions. A single tally compresses those different patterns. Read the result as a broad sign that measured EI gains were frequently reported in teacher-training studies, not as a common effect or a collaboration outcome. Before carrying it into a workplace decision, ask which dimension changed, what comparison was used, and how much change the study reported. The July 2026 review supplies the frequency of favorable findings; those further details determine what the findings can reasonably mean.

Sources: Emotional intelligence training programs for teachers: a systematic review

Which emotional skill was each study trying to change?

The 27 studies in *Emotional intelligence training programs for teachers: a systematic review* did not train or measure one shared version of emotional intelligence (EI). The review found ability, trait and mixed models, a workplace competency model, and social-emotional learning (SEL). Nine studies did not identify an EI model or used another basis, such as mindfulness or communication skills. So ‘EI improved’ can conceal different targets: solving emotion-related problems, describing usual emotional habits, or practicing broader social and emotional competencies.

In an ability model, EI means emotion-related problem-solving performance, such as interpreting an emotional situation or judging how emotions may be regulated. A performance measure scores responses to such problems. Trait EI concerns typical self-perceived emotional dispositions: how people say they notice, understand, or manage feelings. Mixed models bundle emotional and social competencies, traits, or learned skills. The review also identifies Genos, a competency model focused on emotionally intelligent behavior in professional interactions. SEL is broader, including skills such as social awareness and responsible decision-making. The review included SEL-framed programs only when they explicitly targeted and measured EI. These approaches may overlap, but their scores and outcomes are not interchangeable.

A course’s theory and its evaluation tool can point in different directions. Among seven studies explicitly using ability-EI training, two used performance measures, four used self-report tools based on perceived ability, and one used both. One ability-based intervention was evaluated with a trait-EI measure. By comparison, all six explicitly trait or mixed-model studies used conceptually related self-report instruments. These counts describe the teacher studies; they do not establish which approach works better. They do show why ‘ability’ in a program description does not identify what its outcome score represents.

Imagine a course that teaches people to pause, identify an emotion, and choose a response during a tense exchange. A self-report might ask whether participants feel more capable of handling emotion; a performance task might test their judgments about emotion problems. Those are related questions, but not the same evidence. A higher self-rating could reflect confidence or a changed view of one’s habits. A task score concerns responses to test scenarios. Neither alone shows that someone responded differently in a real conversation. This is an illustration, not a case reported by the review.

The broader *Training emotional competencies at the workplace: a systematic review and metaanalysis* shows a related naming problem: it groups interventions targeting EI, empathy, and emotion regulation, and found no eligible emotional-awareness or conflict-management training under its search criteria. That absence is bounded by the review’s definitions and search, not evidence those skills cannot be taught. Its workplace-wide average therefore cannot answer whether a particular course teaches someone to notice frustration, set a boundary, or repair a disagreement.

When weighing training at work, ask what observable skill the course aims to develop and what measure would count as evidence of change. If the aim is steadier responses to criticism, a generic confidence rating may prompt reflection, but it is not direct evidence that feedback conversations changed. A program should name its target and choose a corresponding outcome. Then readers can tell whether the evidence concerns perceived habits, performance on emotion problems, or a behavior the course was designed to practice.

Sources: Emotional intelligence training programs for teachers: a systematic review; Training emotional competencies at the workplace: a systematic review and metaanalysis

Why can a better self-rating and a better ability score tell different stories?

A self-report and an ability test answer different questions. A self-report asks participants to describe how they usually notice, understand, or manage emotion. A performance test such as the Mayer-Salovey-Caruso Emotional Intelligence Test (MSCEIT) asks them to solve selected emotion-related problems. The July 2026 systematic review, “Emotional intelligence training programs for teachers,” found self-report measures in 25 of its 27 studies, performance measures in four, and both approaches in two. Much of its favorable pattern therefore concerns reported emotional functioning; fewer studies tested performance on emotion problems. Neither score directly records how someone handles a difficult exchange at work.

Training can change what a person notices about their habits. After learning to name emotions or distinguish irritation from worry, a participant may use a more demanding standard when rating their skill. Their self-rating could fall even as reflection becomes more specific, or rise with confidence. Those shifts describe self-perception; alone they do not show that performance on an emotion task or behavior in a live interaction changed. A performance measure samples a narrower task under test conditions. It may show whether answers to those problems changed, but cannot stand in for every ordinary workplace situation.

A useful comparison comes from the February 2026 pilot “Effect of the meta-emotions program on enhancing emotional and meta-emotional intelligence in teachers.” It followed 46 teachers in a quasi-experimental pre–post design: 24 took part in seven sessions totaling 21 hours, and 22 were in a comparison group. The study measured emotional abilities with the MSCEIT and separately assessed beliefs and self-evaluation about emotional ability. The researchers reported significant changes in meta-emotional beliefs and self-evaluation, including a reduced tendency to underestimate ability on the test. They found no significant group difference in change on MSCEIT emotional-ability scores.

The pilot makes the review’s measurement imbalance concrete. A program can coincide with changed beliefs about emotion or self-judgment while the selected ability-test score stays similar. That pattern is compatible with awareness shifting before test performance; it does not establish that sequence. Nor does the pilot show that teachers’ interactions improved. Its small, non-randomized groups and test outcomes limit what can be inferred about causes or classroom behavior. The July review and later pilot cover different evidence windows: the pilot adds a post-search comparison, but does not revise the review’s included-study findings.

For someone considering an emotional-skills program at work, ask which result it promises. Better self-understanding, stronger performance on emotion problems, and a change in a specific interaction are separate outcomes. A self-rating may help identify a habit to examine; an ability test samples answers to emotional problems. To support a claim about working together, evaluation needs to examine relevant behavior, such as how people clarify concerns during feedback. Improvement in one measure is evidence about that measure, not a substitute for the others. Ask what was measured, in whom, and whether it matches the intended change.

Sources: Emotional intelligence training programs for teachers: a systematic review; Effect of the meta-emotions program on enhancing emotional and meta-emotional intelligence in teachers: a pilot study

How close did the teacher studies get to measuring work together?

The July 2026 review, “Emotional intelligence training programs for teachers: a systematic review,” found that all nine included studies assessing occupational or work-related outcomes reported a significant improvement in at least one outcome. That is a useful signal: the training studies did not stop at asking whether teachers’ emotional-intelligence scores changed. They also examined outcomes closer to professional life, including self-efficacy, organizational climate, work engagement, communication skills, social competencies, emotional labor, and loneliness at work. But the nine-study count is an index of reported findings, not a common estimate of how much workplace collaboration improved. Those outcomes describe different things. Communication skills concern a person’s capacity or reported conduct in exchanges; work engagement concerns involvement in one’s work; organizational climate describes perceptions of conditions across a workplace. Self-efficacy is confidence about carrying out tasks, while loneliness at work concerns felt social connection. A favorable change in any one could matter to a teacher, but it cannot be substituted for another. For example, a rise in engagement does not establish that colleagues resolve disagreement more constructively, and a more favorable view of organizational climate does not show which interaction changed. The review reports improvements in these separate outcomes; it does not combine them into a collaboration score or a direct test of team performance. The distance between an emotional-intelligence result and “people work together better” has several steps. A training program may first change an emotional skill or a participant’s account of that skill. The skill may then show up in a particular behavior, such as listening through a disagreement or communicating a concern clearly. That behavior might affect a team process, and repeated team processes could contribute to wider workplace outcomes. Each link needs evidence suited to it. A pre/post change in one measure cannot by itself verify the later links, especially when the outcome is self-reported or measured at a different level. This is an interpretation of what the review’s varied endpoints permit us to conclude, rather than a result the review tested as a chain. The broader workplace evidence sets a similar boundary. “Training emotional competencies at the workplace: a systematic review and metaanalysis” says that more research is needed on job performance and constructive conflict management. Its conclusion does not negate the teacher review’s nine positive reports: the reviews cover different samples, interventions, search periods, and outcomes. Instead, it highlights the gap between improvements on selected measures and stronger claims about consequential work behavior. For someone considering development after a difficult meeting or strained handoff, the practical question is therefore specific: did the course measure the behavior at issue, or a more general emotional skill that might support it? If the aim is clearer disagreement, look for evidence about how people communicate during disagreement in the teacher studies reviewed. An EQ change can be a useful part of that account, but it does not answer the collaboration question on its own.

Sources: Emotional intelligence training programs for teachers: a systematic review; Training emotional competencies at the workplace: a systematic review and metaanalysis

Does the workplace-wide average travel to teacher training?

The workplace-wide evidence gives useful context, but no direct estimate for teacher training or collaboration. In the 2024 review, *Training emotional competencies at the workplace: a systematic review and metaanalysis*, researchers analyzed 27 controlled studies and reported an average intervention-control difference of 0.46 standard deviations (95% confidence interval 0.30 to 0.63). A standardized mean difference (SMD) expresses a group difference in standard-deviation units, allowing researchers to combine outcomes measured on different scales. It is not a percentage improvement or a prediction for one person. Because this estimate compares intervention and control groups, it is more informative about training effects than a tally of significant pre/post changes. But the review combined programs targeting emotional intelligence (EI), empathy, and emotion regulation among employed adults in several professions. It found no significant differences by profession or training focus; that does not establish a teacher-specific EI effect or make those programs interchangeable. The July teacher review maps findings in one profession, while the workplace meta-analysis pools controlled results across professions and competencies. Their numbers answer different questions and should not be ranked as competing estimates.

The workplace review also shows how much remains unmeasured. Its search criteria included emotional-awareness and conflict-management training, but no eligible studies on those topics met the review’s requirements. This is a gap in qualifying evidence, not proof that such training cannot help. The search was last updated in November 2022, so the review’s 2024 publication date does not mean it covers later programs. The authors reported high heterogeneity, or substantial variation among results, and low methodological quality overall. Of 50 studies, 18 were rated at critical risk of bias and 28 at serious risk; concerns included self- or peer-reported outcomes and confounding. A pooled average can still describe the included results, but these weaknesses leave uncertainty about how much change reflects training rather than study design, measurement, or program differences. The review also found evidence of publication bias, meaning favorable findings may be more visible in published research than null results. Its authors called for higher-quality research, including randomized controlled trials.

The defensible general conclusion is that measured emotional competencies improved on average across the workplace interventions included. This supports taking skill development seriously, but it cannot forecast that an EI course will improve teamwork by a particular amount. The pooled SMD does not show whether a specific program changed how colleagues handle disagreement, exchange feedback, or repair a strained interaction. Those behaviors require direct measurement. The July review adds a teacher-specific evidence map; the workplace meta-analysis supplies a controlled comparison across broader populations and a wider mix of interventions. Together they support cautious confidence in measured change while leaving collaboration as a distinct question for studies that observe interaction itself.

Sources: Training emotional competencies at the workplace: a systematic review and metaanalysis; Emotional intelligence training programs for teachers: a systematic review

What does one randomized teacher program establish—and leave bundled?

One trial makes the value of a comparison group easier to see. In “Teacher Training Can Make a Difference: Tools to Overcome the Impact of COVID-19 on Primary Schools. An Experimental Study,” 141 primary-school teachers were randomly assigned either to a 14-week training program or to a control group that received no training during the intervention. Random assignment makes it less likely that the groups differed systematically before the course, so a later difference between them is more informative than a simple before-and-after change among participants. The authors report significant group differences in coping with stress, burnout, information and communications technology (ICT) competence, and introducing emotional-intelligence (EI) principles in the classroom.

That is evidence about the program as delivered. Its package addressed several problems at once: stress, burnout, technology competence, and classroom EI practice. The design can support a causal interpretation for the overall package more strongly than an uncontrolled pre/post study, but it cannot tell us which element produced which outcome. Participants may have benefited from the EI content, the stress-management material, the ICT instruction, or their combination. Randomization does not separate ingredients that were delivered together.

The setting also matters. The course was developed in response to COVID-19 disruption in primary schools, where teachers were adapting classroom practice under unusual pressures. “Classroom EI practice” is closer to work behavior than a general self-rating, but it still concerns teachers’ classroom work. It does not directly measure how colleagues manage disagreement, give feedback, or repair a strained project handoff. A course can produce meaningful gains in its intended setting without establishing the same effect in an office team or another profession.

The July 2026 review, “Emotional intelligence training programs for teachers: a systematic review,” helps place this trial in proportion. Across 27 teacher and preservice-teacher intervention studies, only seven used some form of randomization. This makes the 2020 trial a useful example of a stronger design within a field where controlled evidence remains limited. It does not validate every favorable result in the review, and one bundled trial cannot establish an ideal course format for teachers generally. The review’s broader set also includes varied models, training approaches, and outcomes; its study count is not a set of replications of this particular package.

For someone considering workplace development, the practical lesson is to inspect the whole course before crediting one skill label. Ask what the program actually teaches, which outcomes it measures, and whether the measure reflects the interaction you want to improve. A multicomponent program may still be useful even when researchers cannot isolate its active ingredient. But if a provider claims that EI training alone improves collaboration, this trial is not enough to support that claim: it tested a package with several aims in a specific school context, not EI as a stand-alone cause of general teamwork.

Sources: Teacher Training Can Make a Difference: Tools to Overcome the Impact of COVID-19 on Primary Schools. An Experimental Study; Emotional intelligence training programs for teachers: a systematic review

What program features are promising without being a proven recipe?

The July review describes a range of formats, not a winning course design. Across 27 teacher and preservice-teacher studies, programs ran from four hours over two sessions to 32 hours over eight sessions. Some used exercises, practice, and role-play; others used discussion, lectures, or case studies. Both shorter and longer programs reported significant gains in measured emotional-intelligence outcomes. The review notes one exception: the four-hour program was the only study in that pattern without a reported improvement. That contrast cannot show duration caused the null result. Programs differed in more than hours, and the review did not isolate duration.

“Emotional intelligence training programs for teachers: a systematic review” sees more consistent results among structured, multi-session interventions grounded in an explicit framework and including practice or reflection. The authors stop short of prescribing a format because the studies varied in content, measures, and design. Treat this as a prompt for scrutiny, not a comparison proving one recipe superior. Ask which account of the skill guides a course: noticing emotion, making sense of it, regulating a response, or developing broader interpersonal competencies. Then check whether its activities and outcome measure match that aim. A lecture and a role-play can both belong in a course, but give participants different chances to use the skill.

The broader workplace review, “Training emotional competencies at the workplace: a systematic review and metaanalysis,” reports common use of lectures, group discussion, role-play, and other practice. Only 11 of 50 studies included follow-up. In those 11, the average measure fell between post-training and follow-up, with substantial variation across the interventions and measures; the authors conclude ongoing practice or reinforcement may be needed to sustain gains. This does not establish an ideal refresher schedule. It does make evaluation timing part of course design: an end-of-workshop result answers a different question from one checked weeks or months later.

For someone comparing workplace training, three questions follow: what model names the skill, what realistic emotional decision will participants practice, and when will the intended result be checked again? Practice should resemble moments the course claims to address, such as receiving difficult feedback, asking what a colleague needs clarified, or pausing before a heated reply. Evaluation should match that claim. A self-rating can speak to perceived habits; on its own, it cannot establish that a team handles disagreement better. This editorial decision rule follows from the reviews’ measurement and follow-up limits; it is not a formula they tested. It helps distinguish a plausible design from a proven one while allowing different roles to need different practice.

Sources: Emotional intelligence training programs for teachers: a systematic review; Training emotional competencies at the workplace: a systematic review and metaanalysis

What limits the causal and lasting-workplace claim?

The July 2026 review rates its 27 teacher studies as moderate in methodological quality on average, with a mean QualSyst score of 0.65. Seven studies used some form of randomization, and five measured participants again between one and six months after training. A pre/post gain alone cannot show that training caused the change; other events or participant differences may also explain it. The count of studies reporting gains is evidence that improvement was often recorded, not that a particular program produced it. (“Emotional intelligence training programs for teachers: a systematic review.”)

Follow-up means measuring an outcome after training ends. In the teacher review, only five studies did so, across different intervals and designs. That varied set cannot give one stable estimate of how long a typical change lasts. Nor does a later score necessarily answer whether a colleague experienced a change in a difficult conversation: that depends on what the measure assessed.

The broader workplace review supplies a useful counterpoint. Across its intervention studies, it found a moderate effect from post-training to follow-up; the average first follow-up was about 26 days after training. Yet effect sizes were smaller at a second follow-up, and the authors argue that continued practice or reinforcement may be needed. They call for more high-quality randomized studies, noting serious or critical risk of bias in many included studies and possible publication bias. Persistence is plausible, not automatic. (“Training emotional competencies at the workplace: a systematic review and metaanalysis.”)

An older meta-analysis offers broader context. “How Efficient Are Emotional Intelligence Trainings: A Meta-Analysis” combined 24 studies and 28 samples of healthy adults. It reported a moderate pre-to-post change and a stable pre-to-follow-up effect. Those results do not establish durability for teachers, a particular workplace behavior, or collaboration between colleagues.

Taken together, the evidence supports a measured conclusion: emotional-skill scores and related outcomes often improve in training studies, while confidence about cause, persistence, and team-level change remains more limited. The clearest next evidence would come from randomized studies that repeatedly observe the interaction behavior a program aims to change, including after training ends.

Sources: Emotional intelligence training programs for teachers: a systematic review; Training emotional competencies at the workplace: a systematic review and metaanalysis; How Efficient Are Emotional Intelligence Trainings: A Meta-Analysis

What can an individual do with this evidence at work?

Use the July 2026 teacher review as a prompt for an observable experiment at work. Choose a recurring interaction, name one response to practice, and look for examples. A profile can help you select where to look; experience and feedback are needed to judge whether that response helped. For example, before explaining a decision after critical feedback, ask one clarifying question about the concern. This is an illustration, not a tested intervention. After several conversations, consider whether the question helped you understand and respond to the issue. Notice when workload, authority, or unclear responsibilities shaped the exchange. The review reports varied measures and work outcomes, so a change in an EQ measure alone is not evidence that collaboration improved. The private 32-item Emotional Skills Profile separates recent-behavior summaries from judgments on authored scenarios. It is an educational reflection tool, without validated population norms or established ability-test validity. Use it to choose a reflection question, then bring that question into a real conversation. You might ask a colleague: “Could you describe one recent moment when my response to feedback helped clarify the issue, and one when it did not?” Concrete examples give you something to examine and practice.

Sources: Emotional intelligence training programs for teachers: a systematic review; Emotional Skills Profile