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How To Assist Research-Informed Education?
Stephen Gorard, Wenqing Chen
Durham University Evidence Centre for Education
DOI: https://dx.doi.org/10.47772/IJRISS.2025.910000338
Received: 12 October 2025; Accepted: 20 October 2025; Published: 12 November 2025
ABSTRACT
This paper looks at some of the key decisions to be faced in promoting the use of research evidence in policy
and practice – the quality of the evidence to be used, and how that quality can be judged. Once the
policy/school context has determined the issues to be faced, and before the professional judgement of policy-
makers/teachers is used to help carry this out, evidence should presumably inform the decision on how to
address those issues. However, there is a large amount of apparent research evidence on most topics, and much
of that research is very weak. Who decides which evidence is appropriate to use, and how is that judgement
made? This paper illustrates the issues with reference to examples drawn from what works summaries, using a
generic approach to judging quality, and shows that deciding on the relative quality of research evidence is
paramount in whether evidence use will be effective or not. The paper continues by considering the difficulties
for users and others in judging the quality of research, but argues that this problem must be solved. The only
real alternative would be for practitioners to have purported evidence-led approaches thrust upon them, while
policy-makers would presumably continue to evade the imperative to use evidence appropriately themselves.
INTRODUCTION
It sounds sensible to say that education should be informed by research evidence. This is not to say that
evidence should dominate. But that once the policy/school context has determined the issues to be faced, and
before the professional judgement of policy-makers/practitioners is used to help carry out any plan, good
evidence should presumably inform the decision. However, plausible as this sounds, there is as yet little
convincing evidence that using research evidence does improve real-life educational outcomes. This is partly
just because the idea has not been tested much. But it is also partly because it is not clear which bodies of
evidence are trustworthy enough to be used, or even how such a judgement of trustworthiness could be made.
There is a lot of “research” on education, but much of it is very weak – lacking a coherent design, small-scale,
with lots of unacknowledged missing data, and/or using inappropriate measures. This makes it difficult to
identify the best and most robust evidence or bodies of evidence to use, taking time and skill that most research
users currently do not possess. But using any evidence, without consideration of its quality, would mean that
educational outcomes might be unchanged or even harmed by doing something inappropriate. This would
represent a damaging opportunity cost for each generation of students and their one-chance of formal
education. It would then also be difficult to demonstrate the assumed benefits of using evidence for education,
encouraging those stakeholders who are resisting any use of evidence, rather than working to make evidence
use more appropriate, feasible and fruitful.
This paper starts by summarising the current situation for knowledge about evidence use in education. There is
little strong evidence, and this so far shows no impact on student outcomes from evidence use by teachers. In
at least some studies this could be because the primary evidence used by teachers may not actually be robust
enough for real-life use. The paper continues with a discussion of how the robustness of any evidence in
education can be assessed, and then illustrates, with the example of evidence on using enhanced feedback in
the classroom, how important it is that the robustness of primary evidence is assessed before it can be safely
used. This section illustrates the dangers of synthesising bodies of work without consideration of quality, as
had been done by authors like Hattie (1992). The paper then shows via secondary data and an example how
hard it is for users like teachers to be able to judge the quality of existing evidence. It ask what kind of conduit
can be trusted to collate, judge and synthesise evidence for users. The final substantive section suggests a
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ISSN No. 2454-6186 | DOI: 10.47772/IJRISS | Volume IX Issue X October 2025
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somewhat unwelcome alternative, which is that teachers could simply be forced to use and evidence-led
approach. The conclusion considers some more nuanced ways forward.
The push for evidence use
In England, as in many other areas, there is considerable pressure for educators to be research-informed, and
for their practice to be evidence-led. However, even 20 or more years since the inception of a “what works”
revolution, the actual evidence is sparse on how to implement evidence use successfully (Flynn 2019, Nuttley
et al. 2019). A recent very large-scale review of how to get evidence into use found that there was no clear
answer on how evidence transfer from research to use could be best achieved (Gorard et al. 2020a). It has not
even been convincingly demonstrated that using research evidence in education does actually improve
educational outcomes.
Much of the research writing on this topic is conceptual or advocacy work. Finnigan (2023), for example,
suggests strategies and models for research-practice partnerships without testing them. Cherney et al. (2013)
also propose suitable mechanisms but do not test them. Chapman and Ainscow (2019) present a conceptual
framework for evidence use, and Coburn and Talbert (2006) discuss institutional theory.
Only a small proportion of research writing about evidence use is empirical - only a subset of which has tried
to evaluate the impact of evidence-use by education practitioners. And most of that small proportion is very
weak in terms of design or scale.
For example, Washburn et al. (2023) report success from a summer literacy intervention, based on prior
evidence. However, there was no comparator. The improvement was only from pre- to post-intervention
testing, when these Grade 1 to 3 students were also older. Greenwood et al. (2003) claimed success from
school-wide use of an evidence-based literacy approach. But the study was in only one school, and compared
the evidence-based approach with outcomes for students from a different grade level anyway. Dieker et al.
(2009) reported developing Web-based video models of effective instructional practices, as defined by
research evidence, to help train teachers. They discuss the “influence” of such modelling but never tested it,
even with the 11 participants that they mention.
Tortorelli and Bruner (2022) based their work on 17 US elementary teachers trying to use an evidence-based
approach to improve student formative spelling assessments over one year. There was no comparison group.
Taylor et al. (2005) found that US schools (out of 13) with more success in implementing an evidence-based
reform had slightly better improvement in reading. But the study is only correlational, and the result could well
be due to pre-existing differences between schools and teachers.
The list of such small, weakly designed projects is long in this field, as in all fields of education research. Of
course, there is nothing remiss with such small and possible indicative projects in themselves as long as they
are not over-interpreted by their authors or others. The danger lies in them confusing the field, and suggesting
that the answers to how evidence can best be used are known, when they are clearly not.
There is a small amount of research on the impact of evidence use by teachers that is somewhat better than the
examples above. Such research would usually have a counterfactual of a reasonable size, and focus on a
restricted pre-defined range of outcomes. The overall pattern of this work is incomplete, but it is a reasonable
generalisation to say that this strongest work has been the least likely to find any impact of evidence use by
practitioners.
For example, Rose et al. (2017) used two evidence champions in each of 60 schools, trained over four
workshops by academic researchers, to promote evidence use in their schools. Compared to a control group of
59 schools, there was no improvement in student Key Stage 2 reading results after two years, and not even an
improvement in teacher attitudes to research use. This may mean that the approach of using champions is not
effective. Or it may mean that the purportedly evidence-led intervention presented to teachers was ineffective.
In this kind of meta-work it is difficult to distinguish between these two situations, and this emphasises the
importance of only using the best available evidence. Here the intervention used was growth mindset. If the
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complete evidence base for growth mindset is not as strong as Rose et al. imagined then this otherwise
innovative study could not in fact test the impact of research champions (Li and Bates 2020).
Wiggins et al. (2019) used two cohorts of students in 40 schools. The research leaders from each intervention
school were trained and assisted by academic researchers to promote evidence use, via eight CPD sessions,
termly follow-up meetings over two years, a newsletter, website with resources, peer network, and school
visits by the academic team. Each school had to decide on their priorities for improvement, consult the EEF
Toolkit of evidence (see below), implement the most promising approach, monitor progress and change the
approach if it appeared to be not working. The results were minimal. After two years the intervention students
were ahead in maths (effect size 0.04) and English (0.03) by a tiny amount. Here the research evidence to be
used was not specified but its source was. Perhaps the way that the Toolkit is created does not actually yield
the most promising approaches as clearly as it could. And therefore again we cannot tell whether evidence use
does not work, or whether the evidence used was not strong enough.
Lord et al. (2017) looked at the impact of providing schools with research summaries and other evidence-based
resources. The 12,500 primary schools were randomised to four treatment groups and a clean control.
Treatment schools were sent the resources, with or without light touch support, and their subsequent KS2
results monitored. This passive transfer of research evidence made no difference to student outcomes in
English. Schools probably receive too much mail for this approach to work, and schools may anyway need
more support to use the material. Given that the evidence summaries provided were of four different types
from four different expert groups it is less likely that the lack of impact was due largely to a choice of
inappropriate underlying evidence. But this explanation is still possible.
Griggs et al. (2016) evaluated an intervention based on a designated research champion covering five schools
(2,075 pupils), auditing schools’ needs, and providing a variety of generic and targeted development activities.
This did not even increase teachers’ reported use of research, let alone improve student attainment. Speight et
al. (2016) found no evidence of impact on teacher behaviour from encouraging teachers in 10 self-selected
primary schools (teaching 280 pupils) to use modified or summarised research evidence on issues such as
metacognition.
Helmberger (2014) reported that the frequency of teachers’ use of research-based strategies is not linked to
student test success. The nature of the students and their SES was more important in determining outcomes.
Similarly, Edmonds (2007) looked at the results of teachers using research-based comprehension approaches to
teaching social studies. How well the approach was implemented was not related to student outcomes. The key
predictor was students’ reading test scores on entry to the fourth grade. Jacob (2017) found no difference in the
attainment of US students in grades 2 to 5 when teachers in seven schools were randomised to Evidence-Based
Literacy Instruction or a control. One of the problems faced was the difficulty for the teachers of implementing
the approach. Similar issues arose in Andreassen and Braten (2011). This raises the issue of whether an
intervention or policy can ever be considered appropriate if it is not feasible for teachers to implement.
Related to this, See et al. (2016) compared the Key Stage 4 outcomes of nine schools which had all used a
policy of research evidence to inform their own practice, with the progress in 49 other secondary schools in the
same area. The research school headteachers used Hattie’s evidence on enhanced feedback (see below). There
was no impact. It may be feasible for practitioners to use research evidence to inform their own practice.
However, to do it well would require clearer guidance, professional development and modelling of any
strategies suggested. The headteachers all struggled with the primary evidence despite the presence and
assistance of academic researchers. Anyway, like growth mindset perhaps the evidence for feedback is not as
strong as has usually been portrayed.
Assessing the quality of individual studies
Many different schemes have been proposed for assessing the relative trustworthiness of research findings – of
the kind that could be used in education practice. Some are merely checklists of what is in research reports, and
are therefore only a precursor to judging quality (Logullo et al. 2020). Some schemes are intended for users of
research, like That’s a Claim (https://thatsaclaim.org/). Some like the padlock ratings used by the Educational
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Endowment Foundation (EEF) in England help users to judge individual studies, before their results are
synthesised (https://educationendowmentfoundation.org.uk/help/projects/the-eef-security-rating/). Others are
intended more for researchers judging the security of a larger body of work consisting of many individual
studies (Gough 2007), such as systematic reviews of evidence (Madaleno and Waights n.d.). All such
procedures have much in common, with an emphasis on full reporting of large-scale, well-designed studies,
and would presumably lead to similar conclusions.
An especially simple approach for assessing the internal validity of individual studies appears in Gorard
(2021). It is based on the design of each study and how well that fits the research question, the scale or size of
the study, and the completeness and accuracy of the data. There are other issues that could be considered such
as conflicts of interest, or appropriateness of analyses. However, once the first four are decided then the other
factors either generally fall into line as well, or at least cannot make our judgement worse.
Whatever approach is used to judge quality relies on full. comprehensible reporting of that research. For
example, it is not possible to judge whether the research design fits the research question. unless the question
and design are both clearly stated in the report. Judging this is summarised in the first column of Table 1. A
suggested procedure for using the table would be to start with the first column, reading down the design
descriptions until the research you are reading is at least as good as the descriptor in that row. In this the row,
move to the next column and read down the descriptions, if needed, until the study is at least as good as the
descriptor in that row. Repeat this process for each column. For any column, if it is not possible to discern the
quality of the study from the available report(s) then the rating must be placed in the lowest category. Each
study sinks to its lowest level on these four key factors. The final column in the table gives the estimated
security rating for that study. A much fuller description appears in Gorard (2021).
Table 1 - A ‘sieve’ to assist in the estimation of trustworthiness of any research study
Design
Scale
Missing data
Measurement quality
Rating
Strong design for
research question
Large number of
cases per comparison
group
Minimal missing data,
no impact on findings
Standardised,
independent, accurate
4🔒
Good design for
research question
Medium number of
cases per comparison
group
Some missing data,
possible impact on
findings
Standardised,
independent, some errors
3🔒
Weak design for
research question
Small number of
cases per comparison
group
Moderate missing
data, likely impact on
findings
Not
standardised/independent,
errors
2🔒
Very weak design for
research question
Very small number of
cases per group
High level of missing
data, clear impact on
findings
Weak measures, high
level of error, or many
outcomes
1🔒
No consideration of
design
A trivial scale of
study
Huge amount of
missing data, or not
reported
Very weak measures
0🔒
The overall rating suggests a research finding whose trustworthiness is at least at the level of the descriptions
in that row. So 4🔒 suggests a study that is as secure as could reasonably be expected (because no research will
be perfect), and 0🔒 represents a study that is so insecure that it adds nothing safe to our knowledge (the quality
of most actual research in education). Of course, there are no objective criteria for deciding on any rating, or
even on how many categories of ratings there should be. This is true of any such approach to judging quality.
However, this table was the basis for the EEF scheme, has been used by a large number of reviewers
(including teachers) who have found it useful in sifting thousands of studies by quality, and found considerable
agreement between themselves when allocating security ratings independently.
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Why the quality of research matters
Using this sieve approach for illustration, the next section shows why judging the quality of individual studies
matters, and how not doing so can lead to misleading and perhaps harmful use of evidence, especially when
bodies of evidence are summarised.
Enhanced feedback as an example
A widespread and pioneering example of engineering bodies of evidence into greater use for education comes
from Hattie (2008), and subsequent publications. This was perhaps the first real attempt to summarise a huge
body of evidence on key topics for education and to present it in a way that teachers and other users could
understand. In outline, it involved a meta-analysis of all available prior meta-analyses on each topic, estimated
an overall “effect” size for each, and portrayed these in a standard and simple diagrammatic form. The impact
of this work was considerable.
Other researchers and organisations have now produced similar summaries including the What Works Centres,
and the Educational Endowment Foundation Toolkit, in England. The Toolkit aggregates available meta-
analyses on each topic, and portrays the resulting “effect” size as an estimated average number of months
progress for students. It also shows how much any intervention or programme might cost, and gives an
indication of the strength of the evidence so far. The latter is a crucial addition to any summary of evidence.
Hattie (2008) produced an aggregated “effect” size for using enhanced feedback in the classroom of +0.73
(Figure 1). Improving the use of immediate, interactive, formative responses in classrooms would require some
extra development for teachers, and perhaps a period of adjustment for students. It can otherwise be achieved
for no additional costs to schools. Feedback is therefore presented as a feasible and powerful approach to
improved teaching.
Figure 1 – “Effect” sizes from Hattie (2008)
A similar result appears independently in the EEF Toolkit (Figure 2). Here the result is presented as an average
additional six months progress for students, where teachers use enhanced feedback. This is “high impact” for
“very low cost”. In addition, the Toolkit provides an estimate of how strong the body of evidence that lies
behind this finding is. Here, it is four padlocks out of a possible five (where five is a rare and ideal possibility).
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Figure 2 – “Effect” size for feedback from EEF Toolkit
We have chosen to consider feedback in more detail because it has been portrayed as being usefully effective,
relatively easy to implement, and backed up by a sound evidence base. It is therefore a strong example of an
approach that might sensibly be adopted by schools and teachers enthusiastic to use an evidence-based
approach. What follows is an illustration of the difficulties of such an adoption by users. It is not really about
the underlying substantive value of enhanced feedback in the classroom, or its merits relative to any other
approach.
As noted above, both estimates of the value of feedback are based on meta-analyses of existing meta-analyses
of prior studies. This means that the “effect” sizes used in the underlying meta-analyses are aggregated in the
over-arching meta-analyses, weighted by the number of cases in each study. Otherwise, no account is taken of
the research quality of the underlying meta-analyses, and no account at all is taken of the research quality of
the individual studies in those meta-analyses, or their appropriateness to be combined in this way.
This means that the “effect” size of a poor quality study is treated as equivalent to the “effect” size of a very
good study. For example, Hattie (2008) synthesised the results of 74 meta-analyses of feedback, that totalled
4,157 individual studies (reporting 5,755 different effect sizes). This sounds very powerful. However, some of
these studies were randomised control trial designs, appropriate for making clausal claims. Others, indeed most
studies, were not. Some were based on convenience comparisons – teachers that simply were or were not
observed to be using enhanced feedback. It is clear that good teachers (however judged) are more likely to use
feedback. But what is not clear is whether other teachers can improve their teaching by being made to use
feedback. Convenience comparisons cannot address this, and should not have been included in the synthesis.
Or if included they should somehow be weighted to count for less in the outcome than stronger studies do.
One study, for example, had used a MANOVA analysis based on those students who agreed to participate
compared to those who refused, presented as evidence of the impact of the intervention. This is incorrect in
many ways. Comparing the results of volunteers with those of refusers is not appropriate. The groups will
differ in many ways, including motivation, and so any subsequent difference in outcomes cannot be attributed
to feedback. In addition of course, MANOVA like all tests of significance has as a necessary underlying
assumption that all cases have been randomised (i.e. not volunteers).
This latter error is especially important for meta-analyses because many of the underlying studies did not
report “effect” sizes, nor the fundamental findings needed to compute “effect” sizes (such as the mean and
standard deviation of each group). In this large number of reports Hattie (2008) and the EEF Toolkit rely on
the p-values created by significance tests. They did this whether the study met the requirements for the test or
not (the vast majority will not, if only through dropout). Added to this is the issue that p-value thresholds (like
p<0.05) are not “effect” sizes, and that any attempt to convert them to one will create an inaccurate estimate.
P-values themselves cannot tell the reader whether the impact was positive or negative, and if the means are
provided so that the direction of impact is known, then the p-values are not needed.
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Neither the underlying studies, nor the meta-analyses at either level, take missing data into account. This is
crucial because missing data cannot be assumed to arise by chance and always creates the potential for bias
(Gorard 2020). Again, in both summaries, the studies (and meta-analyses) with high levels of missing data are
incorrectly treated as equivalent in the aggregation to studies with little or no missing data.
The “effect” sizes aggregated are not just based on different study designs, and different and often missing
ways of computing them. They are based on different samples and populations. Some studies were conducted
with very young students, others with university students or adults. Some involved only students with special
needs or behavioural disorders. Further, the measures used as outcomes differed widely. Some studies used
standardised tests of academic outcomes (across a wide range of subjects), some bespoke tests, some teacher
assessed, some laboratory-based, and others were observational. Many were not about academic but emotional
or behavioural outcomes. All were simply aggregated regardless, to get that overall +0.73 result. This does not
make any kind of sense.
One of the underlying meta-analyses used by Hattie (2008) was by Kluger and DeNisi (1996). This was
described as “the most systematic” and “included studies that had at least a control group, measured
performance, and included at least 10 participants”. Measuring performance of at least 10 cases, with some
kind of counterfactual sounds like a minimal requirement. But the horrifying implication is that other meta-
analyses in the 74 included by Hattie (2008) had studies with fewer than 10 cases, no comparator, or did not
measure performance.
Additionally, as in any large-scale endeavour some mistakes can creep in. For example, not all of the studies or
“effect” sizes cited in Hattie (2008, Table 1, p,83) can now be found. Hattie (2008) states that the overall effect
size of 54 studies in Lysakowski and Walberg (1982) was +1.13 whereas the original paper reports it as being
+0.97. Hattie (1992) reported that “Skiba, Casey and Center (1986) used 315 effect-sizes (35 studies) to
investigate the effects of some form of reinforcement or feedback and found an effect-size of 1.88”, but it is
later reported as having 35 effect sizes (not studies), and an effect size of +1.24. These differences may be
small, but this kind of thing is a concern in a summary of evidence that is intended for widespread use.
The main point made here is that these hyper-analyses, and many others, are conducted without consideration
of the quality or trustworthiness of the underlying evidence.
An even bigger consideration is whether meta-analyses such as these are even possible. Because an effect size
is a “standard” score, some commentators have suggested that this makes effect sizes comparable between
studies using different measures and approaches. This is not true, and assuming it to be true can be misleading
(Morris 2019). The value of a standardised difference between scores relies on a number of factors such as the
research design, scale of the study, missing data, and the nature and quality of the underlying measurements
(Gorard 2021). This means that effect sizes cannot reasonably be aggregated or averaged, except where all of
the studies involved were of the same design and quality. Effect sizes are also open to publication bias (Chowl
and Ekholm 2018). Effect sizes give no indication of the quality of the study from which they emerged,
although there is evidence that smaller and weaker studies tend to yield larger-seeming effect sizes (Wolf et al.
2020). As ever, research quality matters.
Evidence on studies of feedback
Gorard et al. (2017) report a structured review of single studies related to the use of feedback in primary age
classrooms. The number of studies (19) is less than in Hattie (2008), for example, because the search was
limited to the year 2000 and beyond, and only studies of primary age, with a clear comparator, and academic
outcomes, were included. As shown in Table 2, the majority of the remaining studies show positive impacts
from the use of enhanced feedback. Around a third showed no benefit or worse. Treating all of these studies as
equivalent, apart perhaps from their scale, would lead an analyst to conclude that, on balance, feedback was an
effective and promising approach to improving teaching. And aggregating their results in a meta-analysis, even
taking into account their sample size, would lead to a substantial positive “effect” size.
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Table 2 - Impact of enhanced feedback in primary schools, as assessed by 19 studies found in a systematic
review
Number of studies reporting positive effect
Number of studies reporting no effect or negative effect
13
6
Source: Gorard et al. (2017)
However, if the quality of each study is taken into account, using the sieve above or a similar process, then the
picture changes considerably (Table 3). There are still 13 positive outcomes and six negative or neutral, of
course. Studies rated as zero for quality (adding nothing to our knowledge of the casual impact of feedback)
were excluded. Most studies (14 out of 19) are of the lowest quality. These might be convenience comparisons,
very small, have high levels of missing data or be based on measures tied to the intervention. Of these, 11
reported positive outcomes. This is a common finding of bias in reviews – weak studies tend to have larger and
more positive “effect” sizes. Of the remaining five studies, three have negative results and only two report a
positive outcome. There are no studies with a causal design, large-scale, low dropout, and standardised
outcomes (4🔒) on this topic. Of the two best quality studies, one is positive and one negative. These are
summarised in Table 4.
Table 3 - Quality and impact : studies of feedback
Number of studies reporting positive effect
Number of studies reporting no effect or
negative effect
4🔒 Highest quality
-
-
3🔒 High quality
1
1
2🔒 Medium quality
1
2
1🔒 Low quality
11
3
Table 4 – Highest quality studies of feedback
Reference
Intervention
Smallest cell
Attrition
Effect size
Lang et al. 2014
Formative Assessment
15 schools, 2,000+
pupils
1 school, unknown
number of pupils
0.20
Phelan et al. 2011
Feedback (Year 7)
2,045 pupils
Not reported
0.03
Using the quality of individual studies, in a way that a meta-analysis does not permit, changes the conclusion
that a reasonable reader might otherwise draw from any summary of evidence. Based on quality judgements, it
is not clear that feedback is such a promising and well-evidenced approach to improving teaching. This does
not apply only to enhanced feedback but to any claim based on summarising prior evidence. Others may rate
these studies somewhat differently. There has to be an element of judgement. But the key point here is not a
substantive one about these studies, or of the benefits or not of feedback. The main point is to illustrate how
taking study quality into account can transform an apparently evidence-based picture. And as noted above, if
we want to know whether using evidence can improve policy or practice then we must be sure that the
evidence used is solid.
Who will judge the quality of evidence?
It is clear that any synthesis of the primary evidence on any topic must take the quality of each study into
account. Not to do so is misleading and dangerous. However, it is less clear who can or should make those
judgements, and how they would do so.
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Teachers report lack of support for their use of evidence (Lysenko et al. 2016), often find research inaccessible
(McCartney et al. 2018, Booher et al. 2020), are not equipped by their training to handle research (Mai and
Brundrett 2022), and are even sometimes individually hostile to evidence use. Teachers may imagine that
using evidence removes their autonomy, and jeopardies their vision of what education should be (Holloway
and Hedegaard 2023). In fact, many teachers are sceptical of the value of evidence-led improvement, or to
believe that good teachers are born that way, and this makes them unlikely to use evidence-led approaches
(Nägel et al. 2023). This occurs especially where the teachers have lower academic attainment themselves. In
this context, it is noteworthy that teaching is a profession entered disproportionately by graduates with lower
academic qualifications than many other professions (Gorard et al. 2021).
Teacher confidence in using evidence
We gained access, via the UK Data Service, to the data from an NFER 2010 Survey of Teachers with a focus
on the 3,936 teachers in England with experience in Key Stages 1 to 4. Only 58% of responding teachers said
that using other people’s research was useful, while 24% had not tried it. Of six suggested approaches to
improving their teaching, using research evidence was regarded as the least useful. Instead, reflecting on their
own practice was the most popular (97%). The usefulness of reviewing practice as part of school self-
evaluation was next (73%), followed by using teacher assessment data (71%), and working towards
performance management targets (64%). Even conducting their own research was regarded as slightly more
useful than using external research evidence (61%).
Around 60% of teachers claimed they knew where to find research evidence relative to their teaching. The
biggest barrier to use of external evidence reported by these teachers was lack of time (44%), but only 24%
said that their school encouraged the use of research evidence, and only 16% said that they had regular
opportunities to discuss research with colleagues. However, it is then curious that 34% said they had conducted
their own research in the last year, and 52% were confident in their ability to conduct their own research to
improve their teaching. It is curious because doing research must take more time (and skill to do it right) than
simply engaging with the research of others. Perhaps this means that teachers conducing their own research are
using a very limited range of skills or are not conducting the research to a high and safe standard.
From our own work, it is clear that teachers are not generally ready to make accurate judgements about the
quality of prior research, even when they are enthusiastic about evidence use (Gorard et al. 2020b). Many
believed that research published in a peer-reviewed journal or conducted by experts must be trustworthy. For
example:
All research published in reputable journals is trustworthy
Research published by experts in the field is trustworthy because they have done extensive research in the area
Similarly, many reported that widely-used research or approaches approved by government must be of high
quality. The naivete is, in some ways, astonishing:
Education programmes that are used by many schools must be good otherwise schools would not have used
them
We can trust education programmes recommended by the DfE because they would have been carefully
evaluated
But at heart the problem is that most teachers do not have the time or skills to understand research, and so tend
to rate the importance of evidence lower than their own judgement. For example:
I find it difficult to understand research papers
The most effective teaching method is based on experience
An example of the difficulty of assessing research
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The following example illustrates how hard it is for teachers and other users of evidence to decide which
evidence to trust. It comes from an EEF trial of metacognition. Metacognition, like feedback, is suggested to
be both cheap and effective by EEF, and by Hattie (2008) with an aggregated “effect” size of +0.69. Here the
example comes from one study – a large randomised control trial (over 1,500 students) with a focus on
improving maths attainment. The Executive Summary (p.5) says that “In this trial, pupils who participated in
ReflectED (metacognition) made an average of four months’ additional progress in maths compared to pupils
who did not. For a cheap intervention (as with feedback there is no expense except teacher development) this is
a substantial average gain (Figure 3).
Figure 3 – Summary table for ReflectED
Source:https://educationendowmentfoundation.org.uk/public/files/Projects/Evaluation_Reports/EEF_Project_
Report_ReflectED.pdf
Figure 3 is the overall summary which teachers and school leaders might be expected to use, without looking
any further. It is relatively simple and contains scale, “effect” size, padlock rating (EEF version), and cost
graphics. Readers would have a right to expect that the rest of the report explains and supports this headline.
The main finding is repeated in Figure 4. The “effect” size in column 7 is +0.3. This is perhaps more realistic
than the higher aggregated figures for feedback or metacognition based on hyper-analyses, but still promising.
Figure 4 – Main results table for ReflectED
This is promising until more attention is paid. The figures in brackets in columns 2 and 4 are the number of
cases missing. These are usually students randomised to a treatment but then not providing an outcome score.
While high (over 16% of the original total), these figures are not unreasonable for a large trial. However, they
do mean that the cases are no longer fully randomised – a mathematical necessity in order to compute p-values
or confidence intervals. Therefore, the table can be clarified for users by ignoring or deleting the erroneous
column 8, and the impossible figures in brackets in columns 3 and 5.
The two remaining bits of data are key. The mean for the intervention group (column 3) on the outcome
measurement is 96.87, and the mean for the control is 97.10. Students in the control performed slightly better
than the students given the treatment (training in metacognition). These figures cannot possibly be the basis for
an “effect” size of 0.3. A simple randomised control trial involves randomising a large group of cases to two
groups, so that they are unbiased. If all else remains constant apart from the treatment of the two groups, then it
is warranted to attribute (some of) any difference in outcomes to the differential treatment. The analysis is
simple because the design carries the weight of the warrant.
Here, however, the researchers have not accepted their headline findings (nor provided standard deviations so
that the basic “effect” size can be checked). Instead they have done some modelling – an approach used more
commonly with datasets from passive designs such as cross-sectional, with non-randomised cases. The
researchers have clearly not done this because they accept that their cases are no longer randomised due to
attrition, because they have presented p-values. But they have managed to convert a slightly negative result
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into a strongly positive one, through an analysis that is not clear and that the EEF was not able to explain. They
may, perhaps, be correct in doing so but how can users of evidence be expected to understand what has
happened, and how much should we trust future meta-analyses that simply add +0.3 as the true “effect” size to
their aggregated outcomes, when the control group actually did better in the trial? Note that this study was
given a very high rating of 4🔒 by EEF for its quality, even though it is incomprehensible to its intended
audience.
At the outset, the EEF was a huge improvement on what had gone before, and was known for its relatively
easy to understand reports accessible to users like practitioners. This was possible because, as outlined above,
the power of RCTs makes both analysis and reporting simple. Now though the reports of individual studies
like the one above are so complex that the original audience cannot understand them. So, it is not clear who
they are intended for. In general, teachers will not have the time, inclination or skills to be able to make a
suitable judgement about which studies and which syntheses of evidence to trust.
Conduits between evidence and users
A plausible-sounding solution is that teachers, and other users, are not required to select and interpret robust
research. Instead, there would be a trusted intermediary who would select and translate the most trustworthy
evidence (Brants and Ariel 2023). The model might be like the National Institute for Health and Care
Excellence (NICE) in the UK (Perry et al. 2010), or the “Office for Educational Research” proposed by the
Royal Society/British Academy (2018). Teachers might prefer teacher-related conduits such as their
professional bodies (Miller et al. 2010), or education designers (McKenney and Schunn 2018). Other conduits
might include knowledge brokers, think tanks, and What Works Centres or clearing houses (Edwards 2010).
However, the evidence available does not find that knowledge brokers like this are any more effective at
getting good evidence into use than simple access to research (Dobbins et al. 2009). Their selection of the
evidence to be promoted can be ad hoc, or even biased (Massell et al. 2012). Intermediaries are subject to the
same pressures as users, and so may distort or cherry-pick evidence to suit their user clients, or pursue an
agenda not clearly related to the overall evidence (Malin and Lubienski 2015). Even when the assessment of
core evidence is conducted in good faith, studies have shown that different approaches and expert panels will
reach different decisions about the overall evidence on any topic (Phillips et al. 2020).
The prospect of enforced evidence use
Another way forward would be for users simply to be forced to use evidence-led approaches. This is already
happening in health with interventions implemented at a population level such as the fluoridation of water to
prevent dental caries. This has a lower treatment cost and is more reliable since it requires no additional actions
by the users (Kansagra and Farley 2012). It could be the model for curriculum and lesson resources, and for the
content of textbooks (Prediger et al. 2021). Teachers could then use evidence-based approaches successfully
without knowing what the evidence is (Doabler et al. 2014). This is how much successful impact from research
takes place (Cain and Allan 2017). In terms of conscious teacher actions, an analogue could be the clinical
guidelines for nurses (Thomson et al. 2000), which are required to be evidence-based (Oman et al. 2008), and
their implementation is enforced via audit and the use of report cards (Valentine et al. 2014).
It is likely that if evidence is to improve education successfully then more of such enforced or population-level
measures need to be developed, validated, and implemented. However, this approach still does not solve the
central problem either. It still depends on the highest quality evidence being identified and summarised
appropriately and disinterestedly by someone or some organisation. The examples in this chapter concerning
enhanced feedback, metacognition and others show that even for these widespread approaches the evidence is
not really that clear.
The DfE in England requires that schools show that they are using their Pupil Premium and catch-up funding
effectively, by demonstrating on their websites and through inspections that they “use the wealth of evidence
of ‘what works’, evaluated by the Education Endowment Foundation (EEF)” (Pupil premium: overview -
GOV.UK (www.gov.uk)). This seems appropriate. However, as shown in this chapter, it is not clear that
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schools can totally rely on that kind of evidence, or understand what it means. Nor is it clear that schools do
use evidence in the way intended, rather than searching for evidence to justify their existing preferences and
then putting that on their websites (Gorard 2020b).
A stronger version of the same idea appears in the guidance to providers for initial teacher training in England
(Gov.UK 2022). This guidance is said to be evidence informed, and checked by EEF (again). Teacher trainers
can only use evidence if it is “coherent within the framework”.
A somewhat older example, also from DfE, is the requirement that all primary schools teaching literacy via
systematic synthetic phonics, and only through an agreed provider (Choosing a phonics teaching programme -
GOV.UK (www.gov.uk). A phonics test for children effectively enforces this approach. As with the guidance
for teacher trainers, and the use of the EEF Toolkit, this enforced use of evidence is suitable only if the
evidence for it is really secure.
Suggestions for improvement
In the UK, there is a strong and financially dominating push for all research, especially academic research, to
have “impact” – to make a difference to those it is intended to benefit. This is apparent in appointment,
progression and promotion criteria for university staff, in the demands from UKRI when funding projects, and
in the rules for REF impact case studies that underpin the future QR funding of universities. However, it makes
no sense for all research to have impact. Most education research is of very poor quality and could produce
worse outcomes if actually acted upon. The push for evidence use in real-life must be for the use of high
quality evidence only.
This then is the central question raised by this chapter – who can we trust to judge the evidence that is
available to help improve education? Simply making evidence available does not appear to work (Gorard et al.
2020a). But once it is synthesised, simplified and promoted by others it may no longer be trustworthy, as the
examples in this chapter suggest.
There are several steps that could be taken to help. The evidence base on how best to get evidence into use is
very weak. There is a clear double standard here. Stakeholders have been demanding higher quality evidence
of “what works” but, with the exception of those studies funded by EEF and cited at the start, have not
generally been prepared to fund robust studies of how to translate “what works” into use. Others need to
follow this valuable EEF lead and fund more robust evaluations of evidence into use. We have enough
concepts, maps, theories, barriers and views of stakeholders already. It is worrying that research on this topic is
so poor given that any impact relies on recognising good primary evidence.
In terms of the underlying research that provides evidence to be used in real-life, there is plenty of funding.
What funders could do to help would be to stop funding so much work that is weak and does not lead to
warranted conclusions. It is not clear why so much public money is wasted. Publishers and others could work
harder to make sure that primary research reports are as simple and complete as possible. Users need full
reporting and easy comprehension. Most education research currently has neither. This gives users a plausible
(but incorrect) reason to reject the use of all evidence.
All summaries of evidence would be better if based on explicit judgements of the quality of each individual
study. And meantime, aggregations of evidence that are not based on quality can be safely ignored.
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