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Education Policy Analysis Archives
Volume 11 Number 15 May 8, 2003 ISSN 1068-2341
A peer-reviewed scholarly journal
Editor: Gene V Glass
College of Education
Arizona State University
Copyright is retained by the first or sole author, who grants
right of first publication to the
is a project of the Education
Policy Studies Laboratory.
Articles appearing in
are abstracted in the Current
Index to Journals in Education by the ERIC Clearinghouse
on Assessment and Evaluation and are permanently archived
in Resources in Education.
Teaching Children to Read:
The Fragile Link Between Science and Federal Education Policy
National Institute for Early Education Research
Citation: Camilli, G., Vargas, S., and Yurecko, M. (May 8, 2003). Teaching Children to
Read: The fragile link between science and federal education policy. Education Policy
Analysis Archives, 11(15). Retrieved [date] from http://epaa.asu.edu/epaa/v11n15/.
Teaching Children to Read (TCR) has stirred much controversy among
reading experts regarding the efficacy of phonics instruction. This report,
which was conducted by the National Reading Panel (NRP), has also played
an important role in subsequent federal policy regarding reading instruction.
Using meta-analysis, the NRP found that systematic phonics instruction was
more effective than alternatives in teaching children to read. In the present
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study, the findings and procedures leading to TCR were examined. We
concluded that the methodology and procedures in TCR were not adequate
for synthesizing the research literature on phonics instruction. Moreover, we
estimated a smaller though still substantial effect (d = .24) for systematic
phonics, but we also found an effect for systematic language activities (d =
.29) and tutoring (d = .40). Systematic phonics instruction when combined
with language activities and individual tutoring may triple the effect of
phonics alone. As federal policies are formulated around early literacy
curricula and instruction, these findings indicate that phonics, as one aspect
of the complex reading process, should not be over-emphasized.
The data files that serve as the basis of this article are available for
In 1997 the U.S. Congress directed the Director of the National Institute of
Child Health and Human Development (NICHD), in consultation with the
Secretary of Education, to establish a national panel on research in early
reading development. The panel, now known as the National Reading Panel
(NRP), was charged with conducting a thorough study of the research,
determining what research findings were suitable for classroom application,
and recommending methods of dissemination. Six areas of reading were
eventually examined, and an influential report was released in December
2000. This report, Teaching Children to Read, has stirred much controversy
among reading experts, and both critics and supporters have been highly
visible in national-level venues. Without question, the report has played an
important role in subsequent federal policy regarding reading instruction.
One of the six areas of reading research examined by the NRP was phonics
instruction. According to the NRP:
An essential part of the process for beginners involves learning
the alphabetic system, that is, letter-sound correspondences and
spelling patterns, and learning how to apply this knowledge in
their reading. Systematic phonics instruction is a way of
teaching reading that stresses the acquisition of letter-sound
correspondences and their use to read and spell words…. (NRP,
2000b, p. 2-89).
Using a research methodology known as meta-analysis, the NRP identified
38 experimental and quasi-experimental—meaning a reasonably close
approximation to experimental—research studies on phonics instruction. (A
meta-analysis can be thought of as a quantitative literature review.) Based on
a statistical “averaging” of the outcomes from these 38 studies, the NRP
concluded that their findings “provided solid support” for the conclusion that
systematic phonics instruction is more effective than alternatives in teaching
children to read. Altogether, eleven conclusions were offered regarding the
efficacy of phonics instruction, but the above finding is of prime importance.
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In their deliberations on research findings, the NRP clearly recognized the
ultimate need for instructional decisions to be based on the best empirical
evidence and methods of analysis. The NRP recounted that one theme
“expressed repeatedly,” at a series of five regional public hearings held prior
to its work, was the importance of high standards for choosing evidence
about what works in reading instruction. The NRP interpreted this to mean
that experimental and quasi-experimental studies were most likely to contain
reliable, valid, and replicable findings. However, two aspects of the scientific
method are important and should be distinguished. The review process, i.e.,
meta-analysis, is a set of procedures for distilling conclusions and
generalizations from research studies. In contrast, the “standards of scientific
evidence”—which led the NRP to focus on experimental studies—determine
what evidence will be included in the meta-analytic process.
For the purposes of this review, we were primarily concerned with the
former aspect, that is, the research review process. Most currently available
reviews of the NRP’s study have focused on the interpretation of the results
for phonics instruction while assuming the basic correctness of the
measurement and analytic procedures. We did not make such assumptions;
rather, we designed an independent study in an attempt to reconstruct the
NRP’s central findings. As in other types of scientific investigation,
replicability is a key criterion for judging the credibility of the NRP
meta-analysis, and consequently how seriously we should consider applying
We began with the same 38 studies analyzed by the NRP, but in the course
of our analysis, we deleted one study and added three. We then devised
alternative plans for extracting and analyzing data from 40 studies (38 – 1 +
3 = 40). Based on these analyses, conclusions were drawn and interpretations
made regarding the efficacy of phonics instruction. Though some of the
methodological steps taken by the NRP analysts were retraced, our goal was
to verify whether an independent team of researchers would arrive at
conclusions consistent with those in the NRP report. We did not examine
how the original 38 studies were chosen. It would have been useful to
examine the full range of the NRP’s procedures and findings, including
study selection, but this task would have required resources well beyond our
In our analyses, we found that programs using systematic phonics instruction
outperformed programs using less systematic phonics with d = .24. Though
this effect is statistically significant, it was substantially smaller than the
estimate of the NRP at d = .41. (Roughly speaking, d = 0 means no effect; d
= .5 is moderate; and d = 1.0 is large.) The systematic phonics effect,
moreover, was smaller than the effect for individual tutoring (d = .40).
Students receiving tutoring had one-to-one instruction as opposed to
instruction in small groups or classes. We also found that students who
received systematic language activities did better (d = .29). This effect is
comparable to that of systematic phonics instruction. In addition,
standardized tests tended to give larger effects than locally developed
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instruments (d = .19). Overall, we concluded that there is reason to believe
that these effects are additive. Systematic phonics instruction when
combined with language activities and individual tutoring may triple the
effect of phonics alone.
Though language activities were included in over 30% of the treatment
conditions in the 38 studies, the NRP analysts missed the language effect for
one simple reason: they didn’t look for it. In our opinion, an approach that
recognizes the complexity of reading instruction has the potential to improve
the estimates of average effect sizes in all substantive areas that the NRP
examined including: phonemic awareness instruction; fluency;
comprehension; vocabulary instruction; text comprehension instruction;
teacher preparation and comprehension; strategies instruction; teacher
education and reading instruction; and computer technology and reading
instruction. To obtain more accurate estimates of the full range of variables
that influence reading, analyses would also benefit from, and indeed may
require, a substantially larger sample of studies. In this effort, researchers
with substantive, methodological, and classroom experience—as well as
time and resources—are necessary to find studies, and to propose and test
alternative design strategies. While we applaud the NRP for taking the
challenging and difficult first steps in summarizing the extant knowledge on
reading instruction, it is clear that substantial resources will be required for
completing this essential work.
If the NRP results are taken to mean that effective instruction in reading
should focus on phonics to the exclusion of other curricular activities,
instructional policies are likely to be misdirected. This interpretation of the
data results from a design in which simultaneous influences on reading
interventions were not adequately coded and analyzed. In particular, early
literacy policies are a timely concern, especially as they are interpreted and
applied in the federal Early Reading First Program. Program administrators
and teachers need to understand that while scientifically-based reading
research supports the role of phonics instruction, it also supports a strong
language approach that provides individualized instruction. As federal
policies are formulated around early literacy curricula and instruction, it is
important not to over-emphasize one aspect of a complex process. Fletcher
and Lyon (1998) wrote “a targeted skill cannot be learned without
opportunities for practice and application.” With this common sense
observation in mind, it is not surprising that the research shows a balance of
systematic phonics, tutoring, and language activities is best for teaching
children to read.
In 1997 the U.S. Congress directed the Director of the National Institute of Child Health and
Human Development (NICHD), in consultation with the Secretary of Education, to establish
a national panel on research in early reading development. The panel, which is now known
as the National Reading Panel (NRP), was charged with conducting a thorough study of the
research, determining what research findings were suitable for classroom application, and
recommending methods of dissemination. Five areas of reading were eventually examined,
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and an influential report was released in December 2000. This report (NRP, 2000a),
Teaching Children to Read (Note 1), has stirred much controversy among reading experts,
and both critics and supporters have been highly visible in national-level venues (e.g.,
Manzo, 1998; Pressley & Allington, 1999; Yatvin, 2000; Krashen, 2000, 2001; Garan, 2001,
2002; Ehri & Stahl, 2001; Shanahan, 2001; Coles, 2003). In any case, the report has played
an important role in subsequent federal policy regarding reading instruction (Manzo, 2002;
Manzo & Hoff, 2003).
One of the five areas of reading research examined by the NRP was phonics instruction.
According to the NRP:
An essential part of the process for beginners involves learning the alphabetic
system, that is, letter-sound correspondences and spelling patterns, and learning
how to apply this knowledge in their reading. Systematic phonics instruction is
a way of teaching reading that stresses the acquisition of letter-sound
correspondences and their use to read and spell words…. (NRP, 2000b, p.
Using a research methodology known as meta-analysis, the NRP identified 38 experimental
and quasi-experimental (meaning a reasonably close approximation to experimental)
research studies on phonics instruction. Based on a statistical analysis of the quantitative
results from these 38 studies, the NRP concluded that:
Findings [from the meta-analysis] provided solid support for the conclusion that
systematic phonics instruction makes a more significant contribution to
children’s growth in reading than do alternative programs providing
unsystematic or no phonics instruction. (NRP, 2000b, p. 2-132)
Altogether, eleven conclusions were offered regarding the efficacy of phonics instruction,
but the above finding is of prime importance.
In their deliberations on research findings, the NRP clearly recognized the ultimate need for
instructional decisions to be based on the best empirical evidence and methods of analysis.
At a series of five regional public hearings held prior to its work, the NRP recounted that
one theme “expressed repeatedly” was
The importance of applying the highest standards of scientific evidence to the
research review process so that conclusions and determinations are based on
findings obtained from experimental studies characterized by methodological
rigor with demonstrated reliability, validity, replicability, and applicability.
(NRP, 2000a, p. 1‑2)
Two aspects of the scientific method should be distinguished in this desideratum: the
“research review process,” and the “standards of scientific evidence” that led the NRP to
focus on experimental studies.
In this document, we are primarily concerned with the former aspect, that is, the research
review process. Most currently available reviews of the NRP’s study have focused on the
interpretation of the results for phonics instruction while assuming the basic correctness of
the measurement and analytic procedures. We did not make such assumptions; rather, we
designed an independent study in an attempt to reconstruct the NRP’s central findings. As in
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other types of scientific investigation, replicability is a key criterion for judging the
credibility of the NRP meta-analysis, and consequently how seriously we should consider
applying its findings.
We began with the same 38 studies analyzed by the NRP, but in the course of our analysis,
we deleted one study and added three (Note 2) others originally identified by the NRP. We
then devised alternative plans for extracting and analyzing data from the 40 studies (38 – 1 +
3 = 40). Based on these analyses, conclusions were drawn and interpretations made about
the efficacy of phonics instruction. Though some of the methodological steps taken by the
NRP analysts were retraced, our goal was to verify whether an independent team of
researchers would arrive at conclusions consistent with those in the NRP report. We did not
examine how the original 38 studies were chosen. It would have been useful to examine the
full range of the NRP’s procedures and findings, including study selection, but this task
would have required resources well beyond our means.
Our investigation resulted in several major findings. We obtained a statistically significant
effect for systematic phonics instruction, but one that was substantially smaller than that of
the NRP. Relative to systematic phonics, we also found that individualized instruction (i.e.,
tutoring v. small group or class) had a substantially larger effect while language-based
instructional activities yielded a comparable effect. Finally, we concluded that there is no
reason to believe that these effects are mutually exclusive. Systematic phonics instruction
when combined with language activities and individual tutoring appears to have a much
larger effect than phonics alone.
The remainder of this report consists of seven sections:
Introduction to Meta-Analysis. A brief introduction to meta-analysis is given.I.
Findings of NRP Study. An overview of the NRP findings on phonics instruction is
given along with select results.
Reanalysis: Research Questions and Methods. Questions examined by the current
study are listed, and methodological issues are described.
Re-Analysis: Results. Quantitative results of the present study are given.IV.
Re-analysis: Discussion. The size of the phonics effect is evaluated using results from
other meta-analyses and the moderator effects estimated in the present study.
Meta-analysis and Public Policy. Meta-analysis is discussed as a method for resolving
Conclusions. Conclusions and recommendations are given with respect to integrating
research, especially with respect to phonics instruction.
I. Introduction to Meta-Analysis
Meta-analysis is a public analysis of research findings. It uses publicly available data
sources and reveals explicitly to stakeholders how data are selected and analyzed. Private
knowledge of data or methodology plays no role. Cooper and Hedges (1994) summarized
Two decades ago the actual mechanics of integrating research usually involved
covert, intuitive processes taking place in the head of the synthesist.
Meta-analysis made these processes public and based them on shared, statistical
assumptions (however well these assumptions were met). (p. 11)
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Nearly a quarter century ago, meta-analysis was developed as a set of statistical procedures
for combining the results of many primary studies on a single topic (Glass, McGaw, &
Smith, 1981). Previously, there was no effective way to solve the dilemmas of conflicting
individual or primary studies. With meta-analysis, each study contributes information in a
systematic way, and differences are resolved through statistical analysis.
In a nutshell, meta-analysis is a method of statistically summarizing quantitative outcomes
across many research studies. Cooper and Hedges (1994) described this method as
consisting of five steps:
Problem formulation. Researchers decide whether a sufficient number of studies
exists for a subject of theoretical (e.g., speed of recall) or practical (e.g., class size)
interest. These studies usually investigate treatments or interventions in the framework
of a comparative research design. (Note 3) For example, we might ask whether
students do better in a smaller class (experimental group) rather than a larger class
(control group). This step also involves defining a population of interest (e.g., 4th
graders) as well as measurements or outcomes (e.g., performance on multi-step math
Data collection: Searching the literature. Ideally, all relevant studies would be
obtained for a meta-analysis. To obtain the most exhaustive sample of studies
possible, the researchers must sort through all appropriate reference systems and
publications. Additional studies are frequently added by combing through the
references of obtained studies as well as databases of unpublished studies. The key
idea here is that if a sample of studies is obtained, that sample must fairly represent
the entire population of studies to avoid bias (in the same way that the U.S. Census
must ensure that hard-to-reach subpopulations are fairly represented).
Data evaluation: Coding the literature. Trained researchers must extract information
about each study’s results. A standard list of features (e.g., size of the treatment
groups) is developed prior to reading through the studies, even though some of this
information may not be reported in many studies. Different researchers who record
study information work with common variable definitions so that the information is
reliable and comparable across studies. (Note 4) The determination of what counts as
relevant information for coding purposes should be made by experts who have a
thorough understanding of the treatments, populations, and measurements in question.
Meta-analysis requires a quantitative measure of effect or outcome, but studies using
conceptually similar measures often do not use the same nominal instruments or tests.
Therefore, to be able to combine quantitative treatment-control differences across
instruments, they must be translated to a common scale. For example, if one wanted to
add two measurements, one in centimeters and one in inches, it would be necessary to
convert inches to centimeters (or vice versa). This is what an effect size (labeled as d)
ideally accomplishes. It is a translation of the measured effects from different studies
into comparable units (in this case, standard deviations). More description is given in
Section V on the effect size measure d, but as a rule average effect sizes in
instructional research tend to range from 0 to about ±1.
Analysis and interpretation. A central question for all comparative studies is the
degree to which the experimental group (sometimes called the treatment group)
outperformed the control group. Once effect sizes are computed, statistical analyses
are used to estimate the average d and its margin of error. Analyses also determine
whether certain study features like the duration of treatment influence the effect size.
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Note that estimation of an effect is a different activity than its interpretation. The
meaning of a measurement in centimeters can be quite different depending on, for
instance, whether we are talking about the following distance of automobiles on a
highway or the width of a contact lens.
Public presentation. At every stage of the meta-analysis, records should be kept
regarding procedures. In reporting a meta-analysis, researchers must provide not just
statistical results, but also an account of decisions that led to those results. In addition,
the meta-analysis is not over until the results are linked to the research issues specified
in the first step. In short, the findings must be interpreted and communicated. They
must also be qualified, that is, the researchers help readers to understand limitations of
While the principles of meta-analysis are scientific, the methods it employs are not purely
formulaic. Human judgment is a key element in each of the five steps. In particular,
meta-analysts rely on expert judgment for converting narrative descriptions of a study’s
treatments and subject populations to quantitative measurements. Such coding often requires
substantive expertise in addition to research and quantitative skills. (Note 5)
II. Findings of NRP Study
The subgroup of the NRP for Phonics Instruction described the five steps of its
meta-analysis in Chapter 3, Part II of Teaching Children to Read. In particular, 11 major
conclusions were listed (NRP, p. 2-132 to 2-136). The report is well-summarized by Ehri et
al. (2001, abstract):
A quantitative meta-analysis evaluating the effects of systematic phonics
instruction compared to unsystematic or no phonics instruction on learning to
read was conducted using 66 treatment-control comparisons derived from 38
experiments. The overall effect of phonics instruction on reading was moderate,
d = 0.41. Effects persisted after instruction ended. Effects were larger when
phonics instruction began early (d = 0.55) than after first grade (d = 0.27).
Phonics benefited decoding, word reading, text comprehension, and spelling in
many readers. Phonics helped low and middle SES readers, younger students at
risk for reading disability (RD), and older students with RD, but it did not help
low achieving readers that included students with cognitive limitations.
Synthetic phonics and larger-unit systematic phonics programs produced a
similar advantage in reading. Delivering instruction to small groups and classes
was not less effective than tutoring. Systematic phonics instruction helped
children learn to read better than all forms of control group instruction,
including whole language. In sum, systematic phonics instruction proved
effective and should be implemented as part of literacy programs to teach
beginning reading as well as to prevent and remediate reading difficulties.
For additional detail with regard to the overall results, we give the complete text of the first
conclusion from the NRP report:
Children’s reading was measured at the end of training if it lasted less than a
year or at the end of the first school year of instruction. The mean overall effect
size produced by phonics instruction was significant and moderate in size (d =
0.44). Findings provided solid support for the conclusion that systematic
phonics instruction makes a more significant contribution to children’s growth
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in reading than do alternative programs providing unsystematic or no phonics
instruction. (NRP, 2000b, p. 2-132).
Data analyses supporting these conclusions were based on a straightforward design:
treatment groups receiving systematic phonics were compared to control groups receiving
unsystematic or no phonics instruction. Yet both the experimental and control groups might
receive mixtures of phonics, language instruction, and other activities. The NRP did
examine whether the effect of phonics instruction was influenced by moderator variables,
such as socio-economic status or phonics programs. However, no attempt was made to
classify the degree of phonics or the mixtures of phonics and other language activities in the
groups being studied.
Treatment and Control Group Definitions
In order to understand the overall effect (d = .41/.44), it is necessary to understand the
characteristics of the treatment and control groups (Note 6). The NRP described treatment
groups as including systematic phonics instruction while control groups, though they may
have had some phonics instruction, as having various other types of instruction (NRP,
2000b, p. 2-103) with less systematic phonics. Thus, the effect size generally signifies the
advantage of more versus less systematic phonics instruction:
Whereas some groups were true “no-phonics” controls, other groups received
some phonics instruction. It may be that, instead of examining the difference
between phonics instruction and no phonics instruction, a substantial number of
studies actually compared more systematic phonics instruction to less phonics
instruction. (NRP, 2000b, p. 2-124)
Because almost all children received some instruction in phonics during the course of
comparative studies, this formulation is realistic. However, the degree of phonics instruction
varied from study to study, and it is possible that a treatment in one study could resemble a
control in another.
While we believe that the effect size can be a useful measure in such situations, it must be
realized that any ambiguity in how comparisons vary across studies adds some ambiguity to
the interpretation of the overall or average effect size. The NRP surmised that the effect of
such treatment-control variability might be to underestimate effect sizes. In many cases,
however, children receiving systematic phonics instruction were also receiving activities
consistent with the aims and purposes of whole language. Thus, uncontrolled mixtures might
also serve to overestimate the effects of phonics instruction.
Others have written about the false dichotomy between language and phonics instruction
(e.g., Fletcher and Lyon, 1998). (Note 7) A number of phonics instruction treatments are
described in the NRP report including synthetic, analytic, analogy, onset-rime, phonics
through spelling (NRP, 2000b, p. 2-99), and embedded phonics. Many contain some degree
of language instruction. For example, although “embedded” phonics was not defined in the
NRP report, Foorman, Francis, Fletcher, Schatschneider, and Mehta (1998) described their
“embedded code” treatment as including “whole-class activities such as shared writing,
shared reading, choral or echo reading, and guided reading” (p. 40). In addition the teachers
would “frame a word containing the target spelling pattern during a literacy activity” (p. 40).
Consequently, the treatment is consistent in some important respects with language-based
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instruction, though it can also be described as a type of phonics instruction. While such
treatments defy simple labels, they can be coded on various dimensions that more accurately
describe the “package” of treatment conditions. Analyses can then be undertaken to sort out
the unique effects of various instructional activities and conditions.
Outcome Variables and Units of Analysis
The NRP subgroup on phonics instruction computed effects sizes for dependent variables
that fit into one of 7 categories (also see Table 1) (Note 8):
Dependent Variable Categories.
Category Label NRP Label
1 decoding regular words decoding
2 decoding nonwords nonwords
3 sight word ID word ID
4 spelling spelling
5 comprehension comprehension
6 oral reading oral reading
7 general reading general reading
8 language *
9 phonemic awareness *
10 alphabetic knowledge *
11 vocabulary *
12 writing *
*Category not used in NRP study
For each category within each treatment-control comparison, it is our understanding (NRP,
2000a, p. 1-10) that either mean or median effect sizes were computed for each cohort of
students when results for more than one test instrument were available. In some cases,
studies did not report measures for some categories, in which case the category was left
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blank (i.e., a “missing value”) in Appendix G. At most, one effect size was reported for each
category for each cohort/comparison.
Importantly, measures were excluded from this classification if they were used during (or as
part of) phonics instruction (NRP, 2000b, p. 2-110). Such effect sizes would be expected to
be larger due to “teaching to the test.” No distinction was made between standardized and
experimenter-devised tests. Because standardized tests are targeted to a wider range of
ability, the NRP surmised that they might be less sensitive to change and thus
“underestimate effect sizes slightly” (NRP, 2000b, p. 2-111).
Criticisms of the NRP Meta-Analysis
Three prominent criticisms of the NRP meta-analysis of phonics instruction have spurred
public debate. The first concerns methodology; the second concerns the link between
evidence and conclusions; and the third, the procedures with which research activities were
The first criticism is that a narrow population of children was represented in the 38 studies
that comprised the meta-analysis (Garan, 2002). In particular, Garan argued that many of the
studies did not include “normal readers” and none included groups of advanced readers.
Thus, it would be difficult to generalize the findings broadly across typical populations of
students. The second criticism is that the term “reading” was not used in a consistent
manner; the term reading can refer to simple “word calling” (e.g., a response to the question
“Can you say this word?”), but it can also refer to the ability to derive meaning from
connected text (Yatvin, 2002). If it is said that “Phonics instruction improves reading,” it is
important to know what kind of reading is signified. The third criticism was that the process
used to conduct and report the meta-analysis was flawed. According to Yatvin (2002), the
NRP study on phonics instruction was completed in a very short time. In October, 1999, five
months before the due date, a determination was made that the completion of the study
required resources beyond the capacity of panel members, and it appears that a researcher
who was not a member of the NRP was commissioned to conduct the meta-analysis. (Note
9) Upon completion of the study, again due to time constraints, the panel originally in charge
of designing and conceptualizing the research had only four days to review the final report
before it went to press. Yatvin also observed that only one panel member (Yatvin) had
teaching experience, and thus the NRP had little expertise for the purpose of linking research
findings to practice.
The NRP addressed some of these issues. The 38 studies provided 66 (Note 10)
treatment-control comparisons, and of these, 23 comparisons included normal readers (about
35%). In regard to the second criticism, the NRP found that:
The majority (76%) of the effect sizes involved reading or spelling single words
while 24% involved reading text. The imbalance favoring single words is not
surprising given that the focus of phonics instruction is on improving children’s
ability to read and spell words. (NRP, 2000b, p. 2-92)
Even from this brief quote, it is clear that a necessary distinction must be made between
“word reading” and conceptualizations of reading that imply understanding of connected
text. “Word reading” is just one connotation of reading, yet the distinction isn’t maintained
consistently in formal documents. For example, in Ehri and Stahl’s (2001) rebuttal to Garan
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(2001) (Note 11) they reported that clear evidence was found to support the conclusion that
Systematic phonics instruction was found to be more effective than
unsystematic phonics instruction or no phonics instruction in helping students
learn to read [emphasis added]. (Ehri and Stahl, 2001, p. 18)
One could define reading as “reads single words in isolation,” which would be consistent
with the NRP’s data analyses. But reading could also be defined as “reads connected text,”
that is, sentences or stories. Obviously, one’s sense of the study’s outcome—as represented
in the above quote—depends almost entirely on how reading is defined.
The third criticism was that not enough time was allotted to carry out the charge of
Congress, and that the final report was not subjected to formal review. In fact, the study was
under intense time pressure from inception. According to Yatvin, who wrote a minority
addendum to the final report,
In fairness to the Panel, it must be recognized that the charge from Congress
was too demanding to be accomplished by a small body of unpaid volunteers,
working part time, without staff support, over a period of a year and a half. (The
time Congress originally allotted was only 6 months.) (Yatvin, 2000, p. 2)
Whether the resources and time were sufficient to carry out such an important study is now a
moot issue. The question of interest is whether the meta-analysis conducted by the NRP is
sufficiently reliable and valid for guiding instructional policy in early reading. In the present
study we address the topic of whether the central NRP results can be replicated by a
different team of analysts. A successful replication would provide convincing evidence of
accuracy and allay concerns about study logistics.
III. Reanalysis: Research Questions and Methods
The NRP results were given for 11 central questions regarding phonics instruction. In this
re-analysis, we will be concerned primarily with two of these: “Does systematic phonics
instruction help children to learn to read more effectively than nonsystematic phonics
instruction or instruction teaching no phonics?” (NRP, 2000b, p. 2-132); and “Is phonics
instruction more effective when it is introduced to students not yet reading, in kindergarten
or 1st grade, than when it is introduced in grades above 1st after students have already begun
to read?” (NRP, 2000b, p. 2-133).
Using public—that is, published—accounts of data and methodology, we re-examined the
evidence offered by the NRP on the efficacy of phonics instruction. We designed an effect
size database, recomputed effect sizes for all outcomes available, and then carried out
analyses in which effect sizes were related to study characteristics. One study by Vickery,
Reynolds, and Cochran (1987), which is described in Appendix C, examined the effect of
the same treatment on remedial and nonremedial students. Because there was no control
group, we deleted this study from our database (see inclusion criteria on p. 2-108 to 109 in
NRP, 2000b). We included another three studies that were identified by the NRP but not
included in their meta-analysis. These are described in Appendix A of this report. Thus, our
database was constructed from 40 studies originally identified by the NRP; however, the
merits of the original NRP sample or sample selection process is beyond the scope of the
present study. (Note 12; Note 13)
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Our analytic strategy had several components. We selected a unit of analysis, defined
alternative weighting schemes, and used multiple regression to identify the unique
contributions of variables that moderate the treatment. By moderator variable, we mean a
component of treatment delivery that leads to a stronger or weaker effect. Four new
moderator variables were constructed for specifying the treatment conditions: the degree of
phonics systematicity; degree of coordinated language activities; whether treatments were
regular in-class or pullout programs; and whether basal readers were used. These variables,
which were coded from the research studies by means of rubrics, provided the explanatory
power missing from the simple comparative design used in the NRP analyses. That is, the
NRP design did not fully account for variation in the mixtures and degrees of treatment
delivered to both experimental and control groups. Other moderators were borrowed from
Appendix G of the NRP report. Using regression analysis, we then predicted treatment
outcomes (i.e., effect sizes) with the four new moderators and: the size of the instructional
unit (tutoring, small groups, class); whether treatment conditions were randomly assigned;
whether standardized tests were used; and the age (Note 14) of students.
There are two important design facets in a meta-analysis. The first is a design for data
collection, while the second parallels the usual sense of the word in the phrase experimental
design. That is, there is one design for data collection, and another for analysis. In order to
address the weaknesses of the simple comparative design of the NRP study, we coded
moderator variables, but we also planned for a more complete use of the information within
each of the 40 studies. In particular, we distinguished untreated control groups from
“alternative” treatments, and included both, as described below. This can be likened to
filling out the cells of—or balancing—an experimental design, while the increasing the
number of studies adds to sample size. The recognition of this distinction is not evident in
the NRP analytic plan.
Including Groups for Comparison. As noted above, in each study the NRP designated as the
control a group with less systematic phonics than the treatment group (or groups). Ironically,
this procedure in some cases led to ignoring information from groups labeled as “control” by
the authors of the primary studies. For example, in the study by Lovett, Ransby, Hardwick,
Johns, and Donaldson (1989) three groups were used: the Decoding Skills Program (DS),
the Oral and Written Language Stimulation program (OWLS), and a Classroom Survival
Skills program (CSS). The third group was described as a “control procedure in which
subjects received the same amount of clinic time and professional attention as those in the
experimental remedial programs” (p. 96); however, CSS students received training in
activities that didn’t include reading. It appears that non-treatment controls such as the CSS
group were excluded from the NRP study when programmatic controls like OWLS were
present. Thus, the NRP effect sizes for Lovett et al. (1989) are based solely on the
comparison of the DS to the OWLS program.
In such cases, we computed effect sizes for DS versus CSS and OWLS versus CSS.
However, we coded (with treatment indicators determined by rubric codings) the DS
program as having systematic phonics instruction while the OWLS program was coded as
language-based. This strategy yields an important source of information for disentangling
treatment effects because untreated control groups can provide a common basis for
comparison across studies. The component effects of treatment mixtures may then be more
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Defining Control Groups. More than one control group may have been available for
computing effect size. For example, in Foorman et al. (1998), there were four groups
described as: direct code (DC), embedded code (EC), implicit code-research (IC-R), and
implicit code-standard (IC-S). It appears that the NRP analysts used the IC-S group as the
control even though the authors of the study asserted that comparisons among IC-R, DC, and
EC provided the most relevant information about instructional differences because the IC-R
group controlled for teacher training.
We decided to use the IC-R group for computing effect sizes based on the general rationale
in this paragraph, which we used for all studies. The most valid control was taken as the
group that received the same kinds of treatment activities (e.g., individual attention, duration
of treatment), but not the treatment itself—either language or phonics. This would serve to
control for as many background variables and moderators as possible. For instance, if there
were a choice of control between two groups that did not involve phonics or language
instruction, then we would use this rule to choose the control. We coded systematic
language programs as treatments unless there was not another control group available. In a
study with only a phonics group and a language group, we compared the phonics to the
language group to obtain the effect size, but coded the comparison as being Phonics v.
Language rather than Phonics v. Control. At least three possible classes of comparison
(phonics-control, language-control, and phonics-language) were defined by the rubric
In summary, we included control groups having no systematic phonics or language
interventions, whereas the NRP analysts did not. However, when two control groups were
available, we chose the one most like the treatment group in terms of characteristics
ancillary to the intervention.
Coding Rubrics and Inter-Rater Reliability
We coded the characteristics of both treatment and control groups with rubric indicators.
The rationale for this practice is that coding is a measurement process, requiring inference,
and not a simple reading of a study. Since coding is a measurement process, its scientific
warrant should be established by demonstrating inter-rater agreement. The credibility of the
limited moderators coded by the NRP team was also established by demonstrating high
In Table 2, the rubrics are given that were used to code treatment characteristics. We
distinguished among three levels of phonics instruction; two levels of language; basal reader
usage; and supplemental/pullout versus regular in-class instruction. Rubric codings provide
a richer quantitative description of studies in which instruction is comprised of mixtures of
phonics, language, and other elements. For each study, three independent codings were
obtained. The first codings were given by the authors of the present study, each of whom
had participated in all aspects of at least one previous meta-analysis. None had previously
participated in a study of phonics or whole language instruction, and none had taken a public
position in the phonics versus whole language debates. The second and third codings were
provided, respectively, by an experienced reading teacher and a university professor, each
with a national reputation in reading instruction.
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Rubrics for Coding Treatment Conditions.
ng No information in study to infer code.
0 No specific phonics intervention was given. In most cases, we know that it is
highly probable that students received some kind of phonics activity,
especially for longer interventions. Moreover, even if no phonics instruction
was associated with the treatment delivered, it may have been the case that
other instructional activities (external to the treatment) included phonics. In
short, we were not able to distinguish among these possibilities.
1 Treatment specifically included phonics activities, but treatment activities
were not described in detail as being direct, systematic instruction.
Organized phonics were embedded in language instruction.
2 Treatment was described as including direct, systematic phonics instruction.
It was most often the case that this description specifically included
ng No information in study to infer code.
0 Treatment did not replace regular classroom instruction. In some cases, the
treatment consisted of a supplemental program. For example, students
received treatment at facilities outside of schools (e.g., hospital setting on
1 Treatment was regular classroom instruction, or the treatment completely
replaced regular classroom instruction.
ng No information in study to infer code.
0 Basal reader was not used.
1 Treatment was described as including a basal reader, or it was highly
probable that a basal reader was used. For example, a 4-year treatment
consisting of regular classroom instruction almost certainly used a basal
reader at some point, even if it was not specifically mentioned.
ng No information in study to infer code.
0 No systematic or formal language activities were included.
1 Language-based (non-basal) treatment was given. This may have consisted
of whole word or whole language programs.
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For each effect size computation, both experimental and control groups were coded
according to the rubrics, allowing for the possibility that any group could be coded as having
both phonics and language instruction. However, no phonics treatment labeled as such ever
had less systematic phonics instruction than the group chosen as the control, though both
groups may have had language instruction. In some cases, study information for coding a
rubric was denoted as “not given” by one or more coders. Our guiding principle on this
matter was that evidence of “presence” was required in order to make inferences regarding
the effects of a rubric variable. We converted “not given” responses to zeros. For example, if
a study did not report that basal readers were used, but it was known that the reading
program formally included basal readers (and did during the timeframe of the study), then
assuming their presence was a relatively safe inference. However, for less familiar or
unknown reading programs, it was safest to assume basal readers were not used. In short, the
conservative approach to coding was to require evidence of “presence” rather than
“absence” when linking treatment or moderator indicators to study outcomes.
In Tables 3a-3d, agreement analyses are given for each of the four rubric variables
separately. Under the column labeled “Judges Codings” the number of each possible
combination (i.e., unordered triplet) of three codes, one for each judge, is given. Overall,
there was substantial agreement among coders, given the evidence-of-presence requirement.
In addition to the data in Tables 3a-3d, it is also useful to consider that three raters operating
at random with 95 total comparisons would only have an expected value of about 10-11
matches with a 3-point rubric, and only about 23-24 on a 2-point rubric.
Inter-rater Agreement for the Phonics Rubric
(Cronbach’s alpha for this rubric was .95)
Judges Codings n (95 total) Cumulative Percent Agreement Type
0,0,0 22 23 Perfect
1,1,1 13 37 Perfect
2,2,2 31 69 Perfect
0,0,1 12 82 Adjacent
0,1,1 6 88 Adjacent
1,1,2 4 93 Adjacent
1,2,2 5 98 Adjacent
0,1,2 1 99 ———
unclassed 1 100 ———
Inter-rater Agreement for the Language Rubric
(Cronbach’s alpha for this rubric was .79.)
Codings n (95 total) Cumulative Percent Agreement Type
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0,0,0 55 58 Perfect
1,1,1 11 69 Perfect
0,0,1 9 79 ———
0,1,1 19 99 ———
unclassed 1 100 ———
Inter-rater Agreement for the Basal Reader Rubric
(Cronbach’s alpha for this rubric was .82.)
Codings n (95 total) Cumulative Percent Agreement Type
0,0,0 52 55 Perfect
1,1,1 18 74 Perfect
0,0,1 19 94 ———
0,1,1 5 99 ———
unclassed 1 100 ———
Inter-rater Agreement for the Pullout Rubric
(Cronbach’s alpha for this rubric was .87.)
Codings n (94 total) Cumulative Percent Agreement Type
0,0,0 30 32 Perfect
1,1,1 40 74 Perfect
0,0,1 12 87 ———
0,1,1 11 99 ———
unclassed 1 100 ———
When we encountered a difference among coders, the final code was chosen as the
consensus code in almost all cases. In the few cases where a 2-of-3 majority was not
obtained, codes were averaged. For example, in one comparison the level of phonics was
given codes of 0, 1, and 2, and in this case, the results were averaged resulting in a code of
1.0. Given the “majority rules” principle (Orwin, 1994), the three judges were overruled 24,
25, and 56 times out of 404 coding instances. This translates into overruled percentages of
about 6%, 6%, and 14%, respectively. Thus, an individual judge’s code was retained in a
minimum of 86% of the coding instances. The coefficient alphas were relatively high at .95
(degree of phonics), .79 (presence of language activities), .82 (use of basal readers), and .87
(regular v. pullout program).
The effort in detailing treatment conditions is important for making a strong statistical link
between treatments and outcomes, and would ideally be planned in the design of the study
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and coding protocol. Even so, a dose of realism is required in this effort. The typical study
examined lacked clarity with regard to treatment conditions. It was not uncommon that a
total of three or four sentences were devoted to describing an intervention. Though we feel
69% is an acceptable rate of perfect agreement for level of phonics instruction (with a
reliability of α = .95, see Table 3a), at least part of the 31% of disagreement can be attributed
to the lack of clear descriptions of independent variables. Some “measurement error”
reflects ambiguous descriptions rather than ambiguity inherent in the judgment process.
In the analyses reported below we used, but did not code, other moderator variables in
addition to the rubric indicators. These moderators were borrowed directly from the NRP
study including treatment unit, age/grade, SES, and reading ability. We coded, but did not
obtain inter-rater agreements, for several additional variables for each effect size in our
database including the size (n) of each treatment/comparison group, whether the effect size
was from a randomized study, and whether the effect size was from a standardized
Variable Categories. All effect sizes were recomputed for all available outcome measures
that could be considered as falling into one of the categories in Table 1. In some cases, we
considered outcomes that the NRP did not use, such as alphabetic knowledge, which refers
to how well students can connect phonemes to graphemes. Though these measures fell
outside the range of the NRP’s definition of reading, we felt the information was useful.
Effect Size Computation. Most criticisms and counter-criticisms of the NRP report accept as
their starting point the computed effect sizes as obtained by the NRP analysts. We did not
use the published NRP effect sizes because independent computation is more consistent
with the goals of a validation study based on the merits of replication. Therefore, one major
focus of the present study is computational: Can the general effect size obtained by the NRP
analysts be replicated? However, since we recomputed effect sizes based on a different
design (than the one used by the NRP) for experimental-control comparisons, a one-to-one
comparison was not possible. For this purpose, we devised an approximate method of
comparison (described in Section IV).
Computing an effect size can pose a difficulty with which meta-analysts are all too familiar,
but one that may not be transparent to a consumer of meta-analytic information. In studies
that do not report the necessary information for a simple computation, information must be
pieced together—sometimes using specially designed procedures that may require a number
of assumptions. In this section we review a number of these issues that are pertinent to the
studies on phonics instruction. Although the DSTAT program was used for computations
(Johnson, 1989) by the NRP team, it is often the case that judgments must be made as to
what information to enter into the program; different choices may yield different results even
when calculations are error-free. In a number of instances, the NRP team may not have
appreciated the complexities of computing the effect size d, or they did not provide
rationales for their methods. In this regard, we provide several clarifications below for
facilitating accurate effect size computation.
Although the NRP cites Cooper and Hedges (1994) regarding formulas for computing effect
sizes, the basic formula given by the NRP (NRP, 2000a, p. 1-10) and reproduced below is
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Compared to the pooled effect size estimator (g) given by Hedges (1985, p. 78)
we can see that while the numerators of (1) and (2) are the same, the denominators differ (v
are the degrees of freedom for the experimental and control groups, respectively).
Moreover, it can be shown that the effect size given by (1) is always larger than that given
by the standard formula in (2). The magnitude of this difference is not large, however, and
the NRP calculations appear to have been performed with the correct formula. Nevertheless,
it is important to communicate established procedures in a public document. If a
nonstandard formula is used, a justification should appear in text, but we know of no
justification for the formula in (1). (Note 15)
For the most part, we computed effect sizes in a manner consistent with general
methodological descriptions given in the NRP; the Hedges correction was used in all cases
(Hedges & Olkin, 1985, p. 81). However, because few in-depth details were provided (e.g.,
NRP 2000b, pp. 2-110 to 2-111), we used several additional guidelines for the current study:
a) Standard deviations were pooled across all posttest treatment and control
groups within a cohort of students to create a common denominator. Hedges
effect size adjustment was applied to g to arrive at d (using degrees of freedom
based on the pooled sample).
b) When pretest means were available, effect size numerators were computed as
differential average gains to help control for pre-existing differences. Effect
sizes, according to the first guideline, were then obtained via division with a
common posttest standard deviation. If covariance adjusted effects were
reported, these were used in the numerator instead of the difference between
average gains of treatment and control groups.
c) When testing was carried out on more than two occasions during a treatment
intervention, we computed gains based on pretest and immediate posttest
means. If a treatment spanned several years (or grades), we computed an effect
size for the first year using the second guideline. For each ensuing year
separately, we computed an effect size using the previous year’s posttest as the
following year’s pretest.
d) Effect sizes were computed with custom programming developed for each
individual study rather than using one of the available software products. For
the most part, calculations were based on formulae given by Cooper and Hedges
Units of Analysis. In some cases, classrooms or even schools are used as the units of analysis
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rather than individual students, and this phenomenon did occur in the set of phonics
instruction studies. In this case, classes (or schools) are the units of observation, and class
means comprise the data to be analyzed. The formula given in (2) typically pools individual
level standard deviations that are first calculated with the formula:
When individual observations are group means, however, the estimate of variability, s', is
which is the formula for the standard error of the mean. Upon comparison, it can be seen
that (4) will be smaller than (3) depending on n, which is the class (or school) size.
Therefore, an effect size using class means will be larger than one based on individual
student scores by the multiplicative factor √n. With moderately sized classes, the use of
means can result in substantially larger effect sizes, but these are not comparable to the
effect sizes of other studies whose units of observation are students. To remedy this
disparity, effect sizes must be translated to the individual metric. (Note 16) As we shall see
below, the greatest discrepancy (between a recomputed and original NRP effect size) was
due to a unit of analysis problem.
In the NRP study, effect sizes were computed for each experimental treatment. For example,
if there were one outcome variable, two distinct phonics-based treatments (A and B), and
one control group (C), two effect sizes would be computed (A versus C, and B versus C). If
there were two or more outcome variables in a dependent variable category (e.g., two
spelling tests), the effect sizes for A-C and B-C would be averaged separately within this
Because the NRP reported 66 comparisons from 38 studies, some studies contributed more
than one effect size. For example, one study by Vickery et al., 1987, contributed 8
comparisons—4 grade level cohorts crossed with two levels of remediation. There are a
number of methods for computing the overall average d in this situation. First, one could
compute the simple average across the 66 comparisons given in Appendix G of the NRP
report (NRP, 2000b, pp. 2-169 to 2-175), which results in a mean of .46. This is close to the
value .41 which was reported by Ehri, Nunes, Stahl, and Willows (2001). Implicit in this
procedure is that the Vickery et al. (1987) study receives 8 times the weight of a study that
contributed a single effect size—because it examined 8 distinct treatment-control cohorts.
A second method consists of weighting studies by the total n of the comparison (treatment +
control); in other words, comparisons with larger ns would receive more weight. This was
the method used by the NRP, and results in mean d = .41. In the NRP study, the rationale
was given that
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The subgroups [committees] weighted effect sizes by numbers of subjects in the
study of comparison to prevent small studies from overwhelming the effects
evident in large studies. (NRP, 2000a, p. 1-10).
With this practice, however, large studies overwhelm small studies. For example, in
Gersten, Darch and Gleason (1988), data from 1973-1974 are available for two cohorts of
children with a total n = 242. Treatments were provided at the class level. In contrast, one
comparison described by Gillon and Dodd (1997) contains n = 10 students in two groups.
Given a simple weighting by n, the latter study would have about 1/24th the weight of the
former study. It is our opinion, that this weighting practice should not be automatic;
application of statistical weights necessarily gives studies using classes more weight than
studies using small groups or tutoring.
In a third method for averaging across studies, separate studies are given equal weight. In
this case, the 8 effect sizes in Vickery et al. (1987) would each receive a weight of 1/8; and
the weights would sum to 1.0. This weighting practice would be repeated for all studies
resulting in a set of weights that would sum to exactly the number of independent studies. In
the NRP study, this weighting procedure results in an mean d = .54. (We note that this effect
is larger than the estimate reported in Teaching Children to Read, but stay tuned.) In our
opinion, this approach makes sense when a set of effect sizes is relatively homogenous.
Though Shadish and Haddock (1994) asserted that “all things being equal,” weighting
sample size is the most widely accepted practice, Hedges and Olkin (1985) cautioned that
statistical weights should be considered only in cases with homogenous effects sizes:
Before pooling estimates of effect size for a series of k studies, it is important to
determine whether the studies can reasonably be described as sharing a common
effect size. (p. 122)
Thus, “all things being equal” can be accurately interpreted as “sharing a common effect
A fourth method of weighting represents a compromise between statistically weighting and
equally weighting studies. Let the statistical weights be labeled as WGT1, and let the equal
representation weights be labeled WGT2. A compromise between the two weight types can
be achieved by taking WGT3 = WGT1*WGT2. In the latter approach, consideration is given
both to study representation and sample size. See Table 4 for definitions of the three types of
weighting. For the analyses in the present report, we examine regression estimates derived
from the weighting systems represented by WGT1 and WGT3.
Definitions of Alternative Unit Weights:
Equal Representation, Optimum, and Compromise.
WGT1: If a single study contributed k records to the aggregated database, the equal
representation weight was defined as:
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WGT2: For a particular record in the aggregate database, the total number of
observations for the treatment and control groups was:
The weight was then taken as . Rather than using this approach, we
opted to use the optimum weight defined by Hedges and Olkin (1985, pp. 86
& 110) as:
After examining the distribution of WGT2, we set a maximum value so that
the highest values were no more than 15 times larger than the smallest
WGT3: Given WGT1 and WGT2, this compromise weight WGT3 was computed as:
How studies should be weighted is a critically important issue, because different weighting
methods may give different results. Ironically, the NRP choice resulted in large studies
effects overwhelming those of smaller studies, and the consequences of using this choice
should be carefully considered. In our database of effect sizes, the test of homogeneity was
highly significant (Q = 813.46, 223 df; equivalent z-statistic is roughly z = 27.94) indicating
that the studies did not share a common effect size (i.e., the hypothesis of homogeneity was
rejected). Statistical weights may be inappropriate for the NRP data because of potential
qualitative differences between small and large studies. Moreover, some studies included
multiple comparisons, and statistical weighting gives such studies many times the influence
of studies with a single comparison. A procedure in which studies are given equal weight
may provide the most “equitable” reading of the experimental literature, but a compromise,
which balances representation and statistical precision, may also be useful. Other procedures
may also be defensible, but in any case an explicit justification should be provided.
The issue of weighting involves notions that are fundamental to the ideals of meta-analysis.
Though it can be understood as a statistical issue, weighting can also be understood relative
to the questions “What counts as evidence?” and “How should evidence be accumulated?”
What counts as research in education usually comes in the form of a “study” in which an
author analyzes data and reports conclusions based on those analyses. The results from a
single study may be extremely trustworthy and valuable, and so a problem arises when we
wish to “sum” the evidence in two or more studies. Other things being equal, conclusions
from two studies using the same data would not be valued equally to conclusions from two
independent studies. Yet the problem is not simply to determine appropriate weights for
different studies, but how to understand the role of cumulative evidence vis-à-vis the role of
in-depth knowledge flowing from a single, well-executed study.
Meta-analysis is a systematic method for summarizing the knowledge inherent in a research
literature. Information concerning study outcomes based on unreported or private knowledge
can obviously not add to this summary, even though what is actually learned from a study
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does include unreported and private knowledge. The truth of analytic conclusions can only
be linked to “reports” of empirical investigations. This assertion is very different from the
“garbage in—garbage out” axiom, which implies that a simple “truth in—truth out” model is
possible for synthesizing research studies. The process of establishing warrants for
conclusions is different in meta-analysis than it is in primary research since in published
primary studies authors have direct access to contextual information (e.g., vested interests)
that is not printed, but nonetheless influences reported conclusions. One important
assumption of meta-analysis is that the effects of unreported information will “average out”
across independent studies. This is why fair representation and appropriate weighting
strategies are such important prerequisites to valid conclusions.
The quality of any meta-analysis is fundamentally based on studies that meet inclusion
criteria. In the NRP phonics instruction meta-analysis, the foremost criterion was that
“Studies had to adopt an experimental or quasi-experimental design with a control group.”
(NRP, 2000a, p. 2-108). In addition studies had to appear in a refereed journal after 1970,
had to provide information for testing the efficacy of phonics instruction on reading, and had
to report statistics necessary for computing effect sizes. Having obtained such studies,
information was coded and analyses were conducted. The goal of the NRP meta-analysis
was to identify reliable and replicable results in the area of early reading.
In Appendix B, we provide a perspective on three studies that met these inclusion criteria.
Our goal is to provide readers with a deeper familiarity with the literature, one that extends
beyond the typical boundaries of a meta-analysis. This is important for illustrating how well
the inclusion criteria performed in obtaining methodologically rigorous studies, and for
giving a more salient notion of the confidence with which we can generalize. Indeed, cases
studies were also included in the NRP report because of their descriptive value. We
emphasize that the studies in Appendix B of the present report are given for the purpose of
illustration—issues arise with any study put under a microscope.
The case studies serve to illustrate methodological issues in a number of areas including:
choice of control group, unit of analysis, and study selection criteria. While all three studies
use quasi-experimental designs, a more in-depth examination of these can facilitate a
practical understanding of the variety and limitations in this design approach to reading
research. In our judgment, these studies are representative of, if not of higher quality than,
the entire set of 40 studies.
IV. Re-Analysis: Results
The NRP used cohort comparisons as the unit of analysis, and then applied statistical
weights. (Note 18) We used two strategies for weighting. (Note 19) The first strategy is the
meta-analytic equivalent of “one person one vote” representation. In the second compromise
strategy, we combined statistical (inverse variance or comparison n) weights with equal
representation weights. We remind the reader that the usefulness of weighting—as well as
that of the entire meta-analytic enterprise—depends on how well a set of studies represents
the research literature.
The process of coding resulted in obtaining 491 effect sizes from 40 studies for 12
dependent variable (DV) categories. The Vickery study (described in Appendix C) was
deleted due to lack of a control group. This left 37 original NRP studies, to which we added
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three studies with phonemic awareness outcomes. It appeared to us that the latter three
studies (described in Appendix A), which were identified but not included in the NRP
analysis, met the inclusion criteria of the NRP. Each of these studies, which contributed 7
records total to the database, included at least one reading outcome from categories 1-6 in
Table 1. This database did not include effect sizes from follow-up comparisons. The data
file contained one data record for each effect size. However, single studies often contributed
more than one effect size for a DV category. Moreover, a d for the same outcome variable
category might be computed for more than one cohort within a study. To manage this
redundancy, we aggregated effect sizes to the comparison level within each DV category
within a study. This resulted in a primary analysis file of 225 observations (out of a possible
480, which equals 40 studies multiplied by 12 DV categories); 60 of these represented DV
categories not included in the NRP study. For each case in the aggregated file we included
moderator variables such as duration of treatment, size of the treatment unit, rubric codes,
and the like.
Our unit of analysis was “comparison.” That is, if a study compared one treatment to one
control group, and measured two outcomes, then there were 2 effect size records for one
comparison. In some cases, a study had two treatment groups (T
) and one control
group (C); in this case with two outcomes, there were 4 effect size records (T
v. C, and T
v. C. crossed with two outcomes). Equal representation weights were then obtained as the
inverse of the number of records per study. Multiple cohorts were averaged, if they existed,
within comparison unless the treatment conditions changed across time.
Agreement with the NRP Study
Because of the design difference between the NRP meta-analysis and the present reanalysis,
it is not possible to compare the effect sizes for the two studies directly. However, if effect
sizes are aggregated to the study level (excluding studies with TP = 0), we can examine the
consistency of the two sets of effect sizes. In Figure 1, the scatter plot shows that two studies
(labeled 12 and 53) appear as outliers. Study 53 contained an (d = 8.79) outlier and appeared
to have been removed from most, if not all, NRP calculations. In study 12, effect sizes were
computed by the NRP team with class means; the required conversion of the pooled
standard deviation to the individual metric was not made. With these two studies removed,
= .754 for effect sizes based on the original 7 NRP categories (e.g., Nonwords, Decoding,
etc.) with TP=1 or TP=2.
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Figure 1. Scatterplot of NRP Calculated Effect Sizes and
Our Re-Analysis Calculated Effect Sizes
Again with studies 12 and 53 removed (as well as Vickery et al., 1987), the overall averages
of these two sets of effect sizes do not significantly differ using a paired samples t-test (t =
-.447, p = .658, 33 df). Clearly, the same general information for effect size was obtained,
though a higher level of agreement (correlation) would be desirable. We did not have the
disaggregated NRP effect sizes, that is, Appendix G reports effect sizes aggregated by the
outcomes classification. For the most part, it was not possible to compare specific effect
Level of Phonics Instruction
We computed the overall average d in a different way than the NRP analysts who first
computed an average for each cohort, and then computed a weighted average of these (i.e.,
the cohort averages) across studies. We obtained averages directly from our database, using
“equal study representation” and “compromise” weighting. The analysis of central interest is
the difference between systematic and less systematic phonics, since the latter is what many,
if not most, students already receive. We used the TP rubric variable (scale 0–2) to describe
the level of phonics as a break variable for computing the weighted means given in Table 5.
The group labeled “None/not given” in Table 5 (TP = 0) contains treatments that were
included as alternatives to systematic phonics, including language-based approaches. These
treatments were either not coded by the NRP analysts, or they were used as controls. In the
present study, these were coded as treatments if a separate untreated group was available as a
control. In other words, our “treatments” consist of both phonics and language-based
Breakdown of Effect Sizes by Type of Phonics Delivered in the Treatment Group*
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*Note: Both the compromise (WGT3) and equal representation (WGT1) outcomes sets are
given with sums of weights rather than n. However, for the WGT1 set the sums of weights
are equivalent to the number of studies. All dependent variable categories are included.
A first approximation of the efficacy of systematic phonics is thus given in Table 5 as the
difference between systematic (TP = 2) and less systematic (TP = 1) phonics for which we
obtained d = .514 - .243 = .27, using WGT1. This is about 30% smaller than the magnitude
of the effect reported by the NRP. Table 5 also contains results for WGT2; however, the
results are similar for both sets of outcomes. In the next section, we adjust this effect for
other moderators that are correlated with the treatment variable.
As noted above, we created some moderators and borrowed others from the NRP study
Appendix G. We examined the 15 moderators below, recognizing that a single outcome
could have multiple influences. For this reason, we used weighted multiple regression
analysis to sort out the unique contributions of moderators in predicting effects sizes. In this
analysis, we examined two sets of moderators:
Set I Variable Name Set II Variable Name
Phonics TP Tutoring Tutor
Language TL Duration Months
Basal TB Standardized Test Standard
Replacement TR True Experiment Random
Control Grade Grade
Phonics CP Normal v. At Risk/LD Normal
Language CL Expanded v. NRP DV categories Tag
Set I contains the treatment moderators based on the rubric codings of each comparison
group. Set II contains other aspects of treatment including tutoring (yes or no); treatment
duration; whether the instrument was standardized; whether the experiment was randomized
(yes or no); grade; reader ability category; and whether the outcome fell into one of the
original 7 NRP categories (yes or no).
We conducted the regression analyses with two orthogonal contrasts for degree of phonics
instruction, because effect sizes may not be linear across the categories of TP as suggested in
Table 5. The contrasts TP1 and TP2 were coded as:
TP1 = 2/3 if TP = 0 No Phonics or Unknown
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TP1 = -1/3 if TP = 1, 2 Some or Systematic Phonics
TP2 = 0 if TP = 0 No Phonics or Unknown
TP2 = -.5 if TP = 1 Some Phonics
TP2 = .5 if TP = 2 Systematic Phonics
According to this coding, TP1 represents the difference between treatments coded as having
no phonics or unknown, on the one hand, and treatments coded as having at least some
phonics, on the other. The contrast TP2 represents the specific difference between
treatments coded as having some phonics, and treatments having systematic phonics.
In the regression analyses below, we first entered into the equation the degree of treatment
phonics (TP1 and TP2). We then entered the rest of the 14 (7 Set I + 7 Set II) variables into
the regression using a forward stepwise procedure. (Note 20) We viewed this as a kind of
natural competition of the variables in explaining the results, especially because we took an
agnostic stance with respect to reading theory and the previous NRP results. Results for two
separate regressions are reported below. In Table 6, regression coefficients are given for the
WGT1 weighting method, and in Table 7 for the WGT3 weighting method.
Regression Coefficients for the Analysis Weighted by WGT1,
Regression Coefficients for the Analysis Weighted by WGT3,
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For the WGT1 outcome analysis, the effect of TP1 was d = -.067. This means that treatments
using no phonics or an unknown degree of phonics had less of an effect than programs that
did use a measurable amount of phonics. As shown in Table 6, programs using systematic
phonics instruction outperformed programs using less systematic phonics with d = .241. The
systematic phonics effect, however, is smaller than the effect for individual tutoring (d =
.399). In addition, standardized tests tended to give larger effects (d = .186); studies in which
control groups used language approaches had lower effect sizes (d = ‑.320); and treatments
that used language approaches had larger effect sizes (d = .257). Results for WGT3 analysis
are given in Table 7. The results are similar to those in Table 6 with the effect for systematic
phonics given as d = .188; the tutoring effect was moderately smaller (d = .290); and the
language effects were roughly similar for CL (d = -.221) and TL (d = .228). (Note 21)
Neither analysis provided evidence that randomized experiments give different results than
quasi-experimental studies, or that the results differed for the NRP and the expanded set of
The result for tutoring requires some discussion since it appears inconsistent with the NRP
results. The unweighted effect of tutoring d = 1.09 is reported in Ehri et al. (2001, Table 2),
while the effects for small group and class instruction are given as .44 and .37, respectively.
Thus, the unweighted tutoring effect was documented by the NRP. When studies were
weighted by size, Ehri et al. (2001, Table 1) the effect sizes for tutoring, small group, and
class instruction were .57, .43, and .39, respectively. This change in NRP estimates results
from the weighting scheme used, but also from the deletion of the study by Tunmer and
Hoover (1993). (Note 22) In the present analysis, the deletion of this study results in a
tutoring estimate of d = .21 (p < .007) while the phonics estimate is virtually unchanged.
The Tunmer and Hoover (1993) study also illustrates an important issue for interpreting the
regression results. Recall that there were two treatment groups, and one untreated control
group. The first treatment was the Standard Reading Recovery (SRR). It was modified by
one and only one change: a systematic phonics component was added. This modified
treatment was then given to the second experimental group (MRR). We coded the first group
(SRR) as TP = 1 and the second (MRR) as TP = 2, recognizing the difference between the
two as the best estimate of the systematic phonics effect. This is what the contrast TP2
represents. The difference between the untreated control group and the phonics groups (SRR
and MRR) is the effect estimated by the first contrast TP1.
We examined residuals for the weighted regression analysis and found evidence of one
outlier (standardized residual |z| > 4.5). This case was removed; however, this decision had
very little effect on the model estimates.
Differences Between Outcome Categories
We did not explicitly examine outcomes for dependent variable categories because there
were relatively few studies that contributed to any particular category. Our primary goal was
to replicate results on the overall efficacy of phonics instruction. However, we did examine
residuals from the weighted regression model and test for residual differences between the
DV categories given in Table 1. Using an unweighted analysis (to increase n) and
comparison as the unit of analysis, we found no significant differences, F(11, 212) = .805, p
= .635. This implies that there were no differential effects by DV category. In particular, the
average residual for Spelling was virtually zero. We do not think this result implies that
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phonics instruction is equally effective for all dependent variable categories, but rather that
fine-grain discriminations between different types of reading outcomes require more precise
data than were obtained from the phonics instruction studies.
Effects by Grade, Unit of Instruction, and Duration
We had a special interest in examining variation in effect size by grade/age. This scatter plot
is given in Figure 2, in which it can be seen that in early grades systematic phonics
instruction outperforms typical phonics or no/unknown phonics instruction. However,
differences among these categories are small shortly after grade 3. A conservative reading of
this evidence would indicate that there is no evidence that systematic phonics instruction
outperforms alternative treatments after grade 3. However, the phonics indicator is
confounded with other treatment variables in the early grades, and the strongest inferences
about the efficacy of phonics instruction are obtained from the regression analyses. It should
be kept in mind that the trends represent changes in phonics outcomes rather than changes in
reading comprehension. The outcomes in Figure 2 appear to have an upward trend beginning
just after grade 3. However, the existence of this trend was not verified in the regression
analyses using a quadratic term for grade/age. Thus, the information in Figure 2 should be
interpreted with some caution.
Figure 2. Effect size plotted by grade and degree of phonics instruction.
(On the horizontal axis, the point 0 (zero) represents kindergarten.)
We also plotted tutoring versus other treatment units (i.e., small group and class) in Figure
3. Here it can be seen that tutoring outperforms other instructional unit sizes across the
approximate range of kindergarten to fifth grade. Furthermore, there is a suggestion, that
tutoring has a greater effect in kindergarten and first grade, but also begins to increase again
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after third grade.
Figure 3. Effect sizes plotted by grade and unit of instruction.
(On the horizontal axis, the point 0 (zero) represents kindergarten.)
In Figure 4 effect size is plotted against the duration of treatment in months. Again the
effects of tutoring are superior to those of other units of instruction, but here the effects peak
at about 4 months and decline thereafter. We note that duration here denotes the
chronological length of treatment and does not indicate intensity (e.g., minutes per day).
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Average Effect Sizes for Instructional Methods
Given by Hattie (1999)
Teaching methods dn of ds
Direct instruction .82 253
Figure 4. Effect sizes plotted by duration of treatment in months and unit of
V. Re-analysis: Discussion
Cohen (1988) is commonly cited as suggesting that an effect size of .2 is small, .5 is
moderate, and .8 or above is large. However, the primary criterion for judging an effect size
in educational research is its potential value for informing or benefiting educational practice.
Small effect sizes can be valuable, and likewise large effect sizes can be trivial depending on
the treatment and outcome in question. McCartney and Rosenthal (2000) wrote, "There are
no easy conventions for determining practical importance. Just as children are best
understood in context, so are effect sizes" (p. 175). Average effect sizes only provide
information about whether a program works in a general sense. “A more useful question is
under what circumstances do programs work best?” (McCartney and Dearing, 2002). To
discover these circumstances requires that program characteristics be coded and related to
effect sizes. An average effect size can also be evaluated with respect to other kinds of
educational treatments. While this information does not provide a definitive rule, it does
allow readers to make up their own minds about the practical significance.
In the present reanalysis, the
estimated effect size for systematic
phonics was d = .241/.188 (for
WGT1 and WGT3). This can be
compared to effect sizes reported by
Hattie (1999, Table 7) for various
instructional methods (See Table 8).
The overall average is about .4. In
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Remediation/feedback .65 146
Class environment .56 921
Peer tutoring .50 125
Mastery learning .50 104
Homework .43 110
Teacher Style .42 *
Questioning .41 134
Advance organisers .37 387
Simulation & games .34 111
Computer-assisted instruction .31 566
Instructional media .30 4421
Testing .30 1817
Programmed instruction .18 220
Audio-visual aids .16 6060
Individualisation .14 630
Behavioural objectives .12 111
Team teaching .06 41
* Not given.
addition, Lipsey and Wilson (1993)
examined 302 meta-analyses of a
variety of psychological,
educational, and behavioral
interventions. Interestingly, they
also found that the average
treatment effect (averaging across
meta-analyses) for high quality
studies was .4. The largest ds in the
present study were for tutoring
(.399/.290); and use of language
activities (about .288/.224). In this
context, we would conclude that the
advantage of systematic phonics
instruction over some phonics
instruction is significant, but cannot
be clearly prioritized over other
influences on reading skills. The
regression model suggests,
furthermore, that the effects of
phonics, tutoring and language
activities are additive.
It could be argued that the
systematic phonics effect is actually
larger than the estimate d = .241,
and so the magnitude of the NRP
estimate (about .4) is not an
unreasonable expectation. However,
the studies examined in this
meta-analysis typically did not
accurately describe the degree of
phonics in the control groups. Thus, while the expectation of d = .4 may be plausible, it is
not supported by the data. The effect size d = -.067 (p > .05) for present v. absent/unknown
phonics instruction provides a cryptic message regarding alternative approaches to reading
instruction. This effect is difficult to interpret because it depends on the “unknown
components” of instruction. In the current study, we did not analyze this effect further.
However, for teachers who currently teach some phonics, the expected benefit from a shift
to systematic phonics is d = .241/.188. The present reanalysis suggests that tutoring and
language activities are at least as effective in promoting phonics-oriented reading as
systematic phonics instruction. (Note 23)
Interpretation of the Evidence on Phonics Instruction
The NRP subgroup on phonics instruction concluded that
Findings provided solid support for the conclusion that systematic phonics
instruction makes a more significant contribution to children’s growth in
reading than do alternative programs providing unsystematic or no phonics
instruction. (NRP, 2000b, p. 2-132)
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Based on our reanalysis, the evidence provides ambiguous support for this conclusion.
Systematic phonics instruction did outperform treatment conditions in which a more typical
or moderate level of phonics instruction was provided. But we identified tutoring and
language as critical elements of a reading program in addition to phonics. The data suggest
that a reading effect size has the potential to triple when these elements are added to
systematic phonics instruction. This balance of components is critical in the early grades
because the data suggest that after about third grade phonics instruction may be less
effective. (Note 24) This is more-or-less consistent with the NRP finding that systematic
phonics instruction is most effective in the earlier grades (NRP, 2000b, p. 2-133).
The moderator most strongly related to outcome is the unit of instruction. Tutoring showed a
strong effect throughout grades 1-6 (little data are available to extrapolate further). Though
shorter phonics programs tended to have larger effects, tutoring was also more effective in
this instance. In programs of longer duration, the advantage of tutoring dissipated. Regarding
research methodology, we found that standardized instruments (which were published
and/or normed) tended to show larger effects, contrary to the expectations of the NRP
analysts. This finding, however, was not consistent across the two approaches to weighting
(WGT1 and WGT3).
Finally, the regression results we obtained with two different approaches to weighting were
roughly similar, but the deletion of one case did make a noticeable impact on the estimated
effect for tutoring. This is, unfortunately, the result of a relatively small sample for
conducting analyses. In this situation, there is not a single correct model for obtaining
estimates, but this is not sufficient reason for ignoring the complexities of the data set.
Ultimately, this problem should be resolved by examining larger samples of studies.
VI. Meta-analysis and Public Policy
In the first application of meta-analysis to research on the effectiveness of psychotherapy
(Glass et al., 1981), the researchers confronted issues about research integration: how to
define the population of studies to be synthesized (only published studies, only studies that
met a priori standards of rigor?); how to select and measure the aspects of a study to be
related to the outcomes of that study; how to classify studies and calculate their effect sizes
when the primary researchers failed to report complete evidence; and how to synthesize
outcomes when studies report results for varying sets of outcome measures. (Note 25) The
resolutions of such questions and issues worked their way into the development of
meta-analysis as a methodology that helps social scientists to distill and validate conclusions
from a diverse research literature. This accumulation of research findings is not only helpful
for settling disputes among researchers, but has become an important method for designing
evidence-based public policies.
Meta-analysis would appear to offer great potential for objectivity and even-handedness in
the synthesis of research. Prior to the 1970s, research synthesis had been fraught with
bias—the reviewer selected studies that favored one perspective and cast others out,
typically for ad hoc reasons. Because of its balanced approach, meta-analyses might resolve
polarizing conflicts by making the fullest use of the research literature. The recent report
from the National Reading Panel was likewise motivated in part by the desire to use the best
evidence available to guide instruction in reading. Ironically, this effort has stimulated
controversy regarding what constitutes evidence as well as sound research procedures.
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Meta-analysis is a kind of quality control mechanism in the process of making sense of
numerous individual studies. Yet criteria for the validity of a meta-analysis itself must also
be considered. Is there is a general schema for producing meta-analyses that encourages the
application of new knowledge? In recent years, it has become evident that a more systematic
approach to meta-analysis is required in order for its original ideals to be attained. In the
sections below, we explore issues of scientific due process that appear necessary for
producing high quality meta-analyses, especially in areas of research laden with diverse
philosophies. Included in this discussion are procedural standards, assembly of expert
panels, and peer review.
Standards for Meta-Analysis
The NRP was directed to employ “rigorous research methodological standards” in carrying
out its charge. However, the NRP report included a total of 7 pages (NRP, 2000a, p. 1-5 to
p. 1-11) specifically addressing methodological issues (the seventh page in this section
consisted of 2 references). Issues particular to phonics instruction were covered in an
additional 5 pages (NRP, 2000b, p. 2-107 to p. 2-111). Altogether, less than one page is
devoted to data analysis, and this contains one incorrect formula—a reference to the
software used to compute the effects sizes is provided (which presumably used the correct
formula). An ensuing report of the results by Ehri, Nunes, Stahl and Willows (2001) devoted
just over 1 page to methodological issues beyond study selection. Perhaps this lack of
attention to analytic issues was because the NRP interpreted “rigorous standards” to mean
“rigorous selection criteria” for including studies, but the results of a meta-analysis depend
as much on the rigor of the analytic procedures.
We think it is important for policy-oriented meta-analyses to be designed in advance with
clear descriptions of basic analytic strategies. For example, the Campbell Collaborative
suggests that researchers provide a rationale for why a particular effect size metric was
chosen; under what conditions an effect size will be adjusted for bias; how missing data will
be handled; and so forth. The Campbell Collaborative has been working on a broader set of
criteria for meta-analysis that will play an increasingly important role in establishing the
authoritativeness of a research synthesis. (Note 26)
Constituting Panels and Expert Review
Beyond the Campbell Collaborative principles, there would seem to be an important role of
due process in selecting committees to guide meta-analyses, especially for meta-analyses
that have great potential for influencing teaching practice. The Congressional bills that
directed establishment of the National Reading Panel (SB 939, HR 2192) required that
The Secretary of Education, or the Secretary's designee, and the Director of the
National Institute of Child Health and Human Development, or the Director's
designee, jointly shall… establish a National Panel on Early Reading Research
and Effective Reading Instruction. (3:13-18)
However, the legislation itself provided only two sentences to guide selection of panel
The panel shall be composed of 15 individuals, who are not officers or
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employees of the Federal Government. The panel shall include leading
scientists in reading research, representatives of colleges of education, reading
teachers, educational administrators, and parents. (4:4-9)
Contrast this with the selection guidelines of the Institute of Medicine (IOM), which is an
institutional constituent of the National Academies of Science:
Committees are the deliberating and authoring bodies for IOM reports, although
strict institutional processes must be followed and the peer review process is
independent of the committee. Most committees are consensus committees,
meaning the process is designed to reach consensus on the evidence base and its
implications. Where the published data are insufficient to support a conclusion,
the committee may use its collective knowledge to argue for conclusions. The
committee is formed by identifying the expertise and perspectives necessary to
address the study topic, soliciting and receiving nominations for candidates
from a wide and extensive number of sources, presenting a proposed slate and
alternatives to the IOM leadership group, receiving approval from the IOM
President, and formally requesting appointment from the NRC chairman. A
process of seeking to identify biases and potential conflicts of interest takes
place and may disqualify individuals. (Note 27)
The NICHD and Secretary of Education appear to have conducted a selection process
consistent with the IOM guidelines in constituting the NRP (Note 28); however, there is no
detailed description of the procedure used to choose panelists from about 300 nominees.
Visible selection procedures are important for establishing the perception of balance—that
is, a diversity of theoretical and methodological perspectives—as well as actual balance. An
appropriate mix of talent may facilitate a knowledge base that furthers dissemination of
research findings and improves the design of new research studies. In this regard, the NRP
would have benefited by formal inclusion of one or more methodologists. (Note 29)
Alternatively, the research would have benefited from an officially appointed group of
expert methodologists charged with translating the NRP’s oversight into technically rigorous
guidelines for design as well as data collection and analysis.
We could not find a description of how independent expert review of the final report was
conducted. (Note 30) Moreover, a number of inconsistencies exist between the official
Summary (26 pages in length) of the report and the report itself (Shanahan, 2001). If
Teaching Children to Read had been subjected to a more scrupulous review prior to release,
it would have had more potential to command a consensus. We acknowledge the severe time
constraints under which the report was produced. However, the role of independent review
is to verify and tighten the connections between evidence and summary conclusions. This
process is intended to screen out precisely the kinds of inconsistencies and ambiguities that
appear in the NRP documents.
The impact of meta-analysis is strongly affected by two design decisions. First, the scientific
due process for producing a study is critical to its acceptance. How experts are assembled
and provided with resources is as important as their charge. Secondly, the science itself is
important. There is no single prescription for producing meta-analyses, even though
standards exist for general guidance. In spite of the expertise of research teams, time, and
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resources available, variability among methodological approaches is probable.
Meta-analyses designed to answer controversial questions must anticipate and address this
concern. One strategy might be to assemble two different teams of analysts at the onset of a
study, each carrying out the five steps of meta-analysis. Another possibility may be to
require methods for cross-validation in proposals in response to a formal RFP (request for
proposal). Of course, such elaborate procedures are not necessary for all meta-analyses.
Rather, they are most relevant to those that affect critical policy decisions, such as the
studies conducted by the NRP. In any case, experts (both substantive and methodological)
who do not participate in a study should provide peer review. (Note 31)
Meta-analysis is an effective method of “reading” the literature. Yet for many studies in the
NRP database on phonics instruction, often little detail was given regarding treatment
implementation. The NRP analysts struggled with this issue as evidenced by the number of
missing study descriptors in Appendix G. Without careful description of the treatments, their
implementation, and the populations of students served, it is doubtful that positive treatment
effects can be understood well enough to disseminate to teachers. And without such
description, it may be impossible to understand why some treatments do not work as
expected. Rigorous qualitative work in reading, which the NRP is currently addressing
(Manzo, 2003), has much potential to provide an effective link between theory development,
program implementation, and quantitative research findings.
This reanalysis points to a number of moderator variables that may play a prominent role in
designing phonics instruction. Obviously, two treatments nominally described as phonics
and whole language cannot be directly compared if one uses classroom instruction while the
other employs tutoring. We used regression analysis to sort out the effects of moderator
variables. This provides an improvement to the one-variable breakdowns used in the NRP
report. Based on the regression approach, we found that tutoring and language-based reading
activities had effects at least as large as systematic phonics. In addition, the data suggest
these effects are additive. These results are starkly different from the quantitative results
presented in Teaching Children to Read, but interestingly, they are very consistent with two
Programs that focus too much on the teaching of letter-sounds relations and not
enough on putting them to use are unlikely to be very effective. In implementing
systematic phonics instruction, educators must keep the end [original emphasis]
in mind and insure that children understand the purpose of learning
letter-sounds and are able to apply their skills in their daily reading and writing
activities. (NRP, 2000b, p. 2-96).
Finally, it is important to emphasize that systematic phonics instruction should
be integrated with other reading instruction to create a balanced reading
program. Phonics instruction is never a total reading program. (NRP, 2000b, p.
Despite the manifest consistency of these conclusions with the findings of the present report,
the ideal role of meta-analysis—to solve controversial issues and thus to improve
educational practices—was not directly fulfilled. Two independent teams of researchers
arrived at substantially different interpretations of the same evidence.
If the NRP results are taken to mean that effective instruction in reading should focus on
phonics to the exclusion of other curricular activities, instructional policies are likely to be
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misdirected. This interpretation of the data results from a design in which simultaneous
influences on reading interventions were not adequately coded and analyzed. In particular,
early literacy policies are a timely concern, especially as they are interpreted and applied in
the federal Early Reading First Program. Program administrators and teachers need to
understand that while “scientifically-based reading research” supports the role of phonics
instruction, it also supports a strong language approach that provides individualized
instruction. As federal policies are formulated around early literacy curricula and instruction,
it is important not to over-emphasize one aspect of a complex process.
In our opinion, a sturdier methodology has potential to improve the estimates of the effect
size in all substantive areas that the NRP examined. Analyses would also benefit from,
indeed may require, a substantially larger sample of studies. In this effort, researchers with
substantive, methodological, and classroom experience—as well as time and resources—are
necessary to find studies, and to propose and test alternative design strategies. While we
applaud the NRP for taking the challenging and difficult first steps in summarizing the
extant knowledge on reading instruction, it is clear that more work remains to be done.
This research was completed with the generous support of The Pew Charitable Trusts. The
opinions expressed in this report are those of the authors and do not necessarily reflect the
views of The Pew Charitable Trusts. The authors would also like to acknowledge the
contributions of Mary Lee Smith and Joanne Yatvin.
1. Results of this study were also reported in Ehri, Nunes, Stahl and Willows (2001), and
Ehri, Nunes, Willows, Shuster, Yaghoub-Zadeh, and Shanahan (2001).
2. Details of this selection process are given in Section III.
3. Meta-analysis can also be performed with studies that that do not examine treatment
interventions (e.g., Hunter and Schmidt, 1990). We do not consider other genres of
4. Meta-analysis is a labor-intensive research activity. It is common to assemble research
teams to facilitate the identification and coding of studies within a reasonable amount of
time. However, different coders should record the same study information with a limited
margin of error.
5. Readers are referred to Hunt (1997) for an accessible account of the story of
6. The first estimate d = .41 is for outcomes at the conclusions of programs. The second
estimate d = .44 is for end of program or end of school year, for programs lasting longer
(Ehri et al., 2001, p. 414).
7. Fletcher and Lyon (1998) wrote “In many studies, the research was designed to evaluate
the degree of explicitness required to teach word recognition skills. Instruction in word
recognition skills, however, occurs along with opportunities for applications to reading and
writing, exposure to literature, and other practices believed to facilitate the development of
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reading skills in proficient readers. This reflects one of the oldest observations of any form
of teaching or training—a targeted skill cannot be learned without opportunities for practice
and application.” (pp. 59-60).
8. On p. 2-110 the outcome categories are given, but we could find no rationale for this
9. Yatvin (2002) reported that “As time wound down, the effects of insufficient time and
support were all too apparent. In October 1999, with a January 31 deadline looming,
investigations of many of the priority topics identified by the panel a year earlier had not
even begun. One of those topics was phonics, clearly the one of most interest to educational
decision makers and to the public. Although the panel felt that such a study should be done,
the alphabetics subcommittee, which had not quite finished its review of phonemic
awareness, could not take it on at this late date. And so, contrary to the guidelines specified
by NICHD at the outset, an outside researcher who had not shared in the panel's journey was
commissioned to do the review” (p. 368).
10. These did not include follow up comparisons.
11. Garan (2001) shared Yatvin’s concern that the NRP did not use a consistent definition of
reading. Garan also criticized the NRP meta-analysis for being limited to a small number of
studies and for conceptually dissimilar dependent variables. The latter two points, in our
view, are problems common to both meta-analysis and narrative review. The degree to
which they limit generalizability varies and cannot be determined a priori.
12. A re-examination that began at the problem formulation stage and proceeded to locating
relevant studies would provide a more stringent criterion for replicability. It would also be
significantly more costly. Though we skipped these two steps, we would agree that problem
formulation and data collection significantly shaped the NRP’s study.
13. We excluded follow up comparisons, that is, any measurements taken after post-test
measurements were excluded from the analyses.
14. While some studies reported age, others reported grade. We converted all results to an
approximate grade metric based on the formula grade = age – 5.
15. This formula does not appear in Cooper and Hedges (1994). See Table 16.2 on p. 237.
16. In this simple case, one divides the class-level effect size by √n.
17. We say “distinct” because each cohort involved different groups of students.
18. The data analysis described on p. 1-10 appears to use total ns as weights rather than the
inverse variance weights described by Hedges and Olkin (1985) on pp. 86 & 110.
19. In the future “pure” statistical weights might be usefully applied when homogenous
subsets of effect sizes are identified.
20. We used a highly conservative approach in the forward stepwise selection of
independent variables. We required a p-value of .01 (PIN) to enter and a p-value of .05
(POUT) for removal.
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21. Organized language activities were observed in about 30% of both experimental and
control comparisons. Note that effective language activities in the experimental group will
make the effect size larger, while effective language activities in the control group will
make the effect size smaller. Thus, the two estimates logically have the opposite sign.
22. The NRP deleted one study (Tunmer and Hoover, 1993) with d = 3.71 in obtaining the
average effect size for tutoring. The value 3.71 arose as the average of 4 effect sizes for
WordID (2.94), Spelling (1.63), Nonwords (1.49), and Oral Reading (8.79). It is obvious
that the last effect size is an extreme outlier, and the NRP sensibly deleted this in its
computations for tutoring. We surmise that this effect size was properly deleted from other
computations. We also deleted this effect size (8.71) from our computations, but we
included other effect sizes from this study, which ranged from .96 to 3.18.
23. It is interesting that the effect sizes for experimental and control group language
instruction are very nearly the same (taking into account reversed signs), which supports the
internal design consistency of the treatment codings.
24. The gap is nearly zero at third grade, but widens somewhat at higher grades. Students in
later grades do benefit, but are more likely to represent populations of reading disabled
25. Material on the origins of meta-analysis was provided by Mary Lee Smith in a personal
26. The Campbell Collaboration is an emerging international effort that “aims to help people
make well-informed decisions by preparing, maintaining, and promoting access to
systematic reviews of studies on the effects of social and educational policies and practices.”
More information is available at http://www.campbellcollaboration.org.
27. This information is available at
28. “Applicants who had taken strong stands supporting or opposing any particular
approaches to reading instruction, or with a financial interest in commercial reading
materials, were not considered, according to Duane Alexander, the director of the National
Institute of Child Health and Human Development, who helped select the panel” (Manzo,
2000). In addition, panelists could not be employees of the Federal government.
29. Two expert consultants in methodology were introduced to the Panel in late January,
1999. It appears that both were made available to NRP members on an as needed basis. This
information is available at
www.nationalreadingpanel.org/NRPAbout/Panel_Meetings/01_21_99.htm. Note that the
original deadline for the NRP report was January 31, 1999.
30. There appears to be a collection of documents in which the NRP’s interactions are
recorded. We do not know if this archive is available for public examination (see Yatvin,
31. The Campbell group, referenced above, provides design review as a service. It does not
appear to review drafts of final reports.
40 of 51
32. The K-3 NFT group size in the Gersten et al. (1988) study is reported as 45. Official
documents give n = 21.
33. This model was sponsored by the Southwest Educational Development Laboratory. It
stressed a developmental approach geared to children whose primary language was not
English. In this approach primary language and cultural background are essential to the
34. The next five effect sizes are from Camilli (1980). They are covariance adjusted based
on a modified linear model that includes a linear selection rule.
35. This model was sponsored by the City University of New York. Rather than didactic
methods, direct interaction with other children was the primary method of learning.
Instructional games developed skills in the areas of language, reading, and arithmetic.
36. This model was sponsored by the University of Florida. The primary emphasis was on
motivating parents, and teaching them to set and attain their children’s educational goals.
Parents spent time as instructional assistants as well as visiting other FT parents.
37. This model was sponsored by Northeastern Illinois University. Entry language and
experience of the children are built upon using a method of language elicitation focusing on
the use of oral language in all curriculum areas.
38. Dissertation study, see references.
39. For all reading and spelling outcomes, the amount of growth (linear component) in each
class was negatively related to initial PPVT-R standard deviations (using class as the unit of
Camilli, G. (1980). A Reanalysis of the Effect of Follow Through on Cognitive and
Affective Development (University of Colorado, Boulder). Dissertation Abstracts
International, DAI-A 41/04, p. 1366, Oct 1980.
Coles, G. (2003). Reading the Naked Truth. Portsmouth, NH: Heinemann.
Ehri, L., Nunes, S., Willows, D., Schuster, B., Yaghoub-Zadeh, Z., and Shanahan, T. (2001).
Phonemic awareness instruction helps children learn to read: Evidence from the National
Reading Panel's meta-analysis. Reading Research Quarterly, 36, 250-287.
Ehri. L., Nunes, S., Stahl, S., and Willows, D. (2001). Systematic phonics instruction helps
students learn to read: Evidence from the National Reading Panel's meta-analysis.
Review of Educational Research, 71(3), 393-447.
Ehri, L. & Stahl, S. (2001). Beyond the Smoke and Mirrors: Putting Out the Fire. Phi Delta
Kappan, 83(1), 17-20.
Fletcher, J. M., & Lyon, G. R. (1998). Reading: A research-based approach. In W. M. Evers
(Ed.), What's gone wrong in America's classrooms (pp. 49-90). Stanford, CA: Hoover
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Foorman, B. R., Francis, D. J., Fletcher, J.M., Schatschneider, C., & Mehta, P. (1998). The
role of instruction in learning to read: Preventing reading failure in at-risk children.
Journal of Educational Psychology, 90, 1-19.
Foorman, B., Francis, D., Novy, D. & Liberman, D. (1991). How letter-sound instruction
mediates progress in first-grade reading and spelling. Journal of Educational
Psychology, 83(4), 456-469.
Garan, E.M. (2001). Beyond the Smoke and Mirrors. Phi Delta Kappan, 82(7), 500-506.
Garan, E.M. (2002). Resisting reading mandates. Portsmouth, NH: Heinemann.
Glass, G. V, McGaw, B., & Smith. M.L. (1981). Meta-Analysis in Social Research. Beverly
Hills: SAGE Publications.
House, E., Glass, G., McLean, L., & Walker, D. (1978). No simple answer: Critique of the
FT evaluation. Harvard Educational Review, 48(2), 128-160.
Hunt, M. M. How Science Takes Stock: The Story of Meta-Analysis. (1997). NY: Russell
Hunter, J.E. & Schmidt, F.L. (1990). Methods of Meta-Analysis. Newbury Park, CA: SAGE
Krashen, S. (2000, May 20). Reading Report: One Research’s ‘Errors and Omissions.’
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Krashen, S. (2001). More smoke and mirrors: A critique of the National Reading Panel
(NRP) report on fluency. Phi Delta Kappan, 83(2), 118-22.
Layzer, J., & Goodson, B. (2001). National Evaluation of Family Support Programs.
Cambridge, MA: Abt Associates, Inc.
Lipsey, M.W. & Wilson, D.B. (1993). The efficacy of psychological, educational, and
behavioral treatment: Confirmation from meta-analysis. American Psychologist, 48(12),
Lovett, R., Ransby, M., Hardwick, N., Johns, M., & Donaldson, S. (1989). Can dyslexia be
treated? Treatment-specific and generalized treatment effects in dyslexic children’s
response to remediation. Brain and Language, 37, 90-121.
Manzo, K.K. (1998, February 18). New National Reading Panel faulted before it’s formed.
Education Week, 27(23), 18.
Manzo, K.K. (2000, April 19). Reading Panel Urges Phonics For All in K-6. Education
Week, 19(32), 1 & 14.
Manzo, K.K. (2002, January 30). New Panels to Form to Study Reading Research.
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McCartney, K. & Rosenthal, R. (2000). Effect size, practical importance, and social policy
for children. Child Development, 71, 173-180.
McCartney, K. & Dearing, E. (2002). Evaluating Effect Sizes in the Policy Arena. The
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Report of the National Reading Panel: Teaching Children to Read: An Evidence-Based
Assessment of the Scientific Research Literature on Reading and its Implications for
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(Eds.). The handbook of research synthesis. New York, NY: Russel Sage.
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school setting. Annals of Dyslexia, 37, 189-200.
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About the Authors
10 Seminary Place
New Brunswick, NJ 08901
43 of 51
Gregory Camilli is Professor in the Rutgers Graduate School of Education. His interests
include measurement, program evaluation, and policy issues regarding student assessment.
Dr. Camilli teaches courses in statistics and psychometrics, structural equation modeling,
and meta-analysis. His current research interests include school factors in mathematics
achievement, technical and validity issues in high-stakes assessment, and the use of
evidence in determining instructional policies.
As Assistant Professor at Kean University, and Adjunct Professor at Touro College and
Seton Hall University, Sadako Vargas has taught in the areas of research methods and
occupational therapy. Her interests lie in the use of meta-analysis for investigating
intervention effects in the area of rehabilitation specifically related to pediatrics and
occupational therapy intervention.
Michele Yurecko is a Ph.D. student in Educational Psychology with a concentration in
educational measurement at the Graduate School of Education, Rutgers University. Her
academic interests include the study of research methods and design applied to the field of
education, and the intersection of educational research, testing and public policy.
63 Barr, R. (1974). The effect of instruction on pupil reading strategies. Reading
Research Quarterly, 10, 555-582.
This study compared a phonics with a sight word method of instruction. Word
learning tasks, word recognition, and comprehension were tested. The process by
which subject were assigned to groups was not described, but it was reported that
the groups did not differ in age or readiness as measured by the World Learning
Tasks. Outcome variables for effect size computation were reported in terms of
substitution errors on word reading tasks.
65 Peterson, M.E. & Haines, L.P. (1992). Orthographic analogy training with
kindergarten children: Effects on analogy use, phonemic segmentation, and
letter-sound knowledge. Journal of Reading Behavior, 24, 109-127.
This study examined the effect of teaching orthographic analogies based on words
that rhyme. Children were tested on segmentation ability, letter-sound knowledge,
and reading words by analogy. Subjects were stratified on ability measures, and
then assigned by odd and even numbers (sequential ranks) to treatment and
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68 Gillon, G. & Dodd, B. (1997). Enhancing the phonological processing skills of
children with specific reading disability. European Journal of Disorders of
Communication, 32, 67-90.
This study compared a 20-hour phonological training program to two groups
tested in a previous study published in 1995. We used the original 1995 data in
which a group receiving 12-hour phonological training was compared with a
group receiving 12-hour semantic syntactic training. Groups were tested with the
Neale Analysis of Reading Ability – Revised.
Case Studies of Three Selected Studies
Gersten, Darch, & Gleason (1988)
This study used select data from the Follow Through (FT) Planned Variation Experiment,
which aimed to increase the achievement and self-concepts of children from economically
disadvantaged backgrounds. To give some background, the Follow Through program was
intended to pick up where Head Start ended, and maintain presumed academic gains from
Kindergarten to third grade. According to White et al. (1973, Volume II)
[Follow Through] is intended to be a comprehensive project offering
educational, medical and dental, nutritional, social, and psychological services
to children previously enrolled in Head Start. Follow Through uses a strategy of
“planned variation” in approaches to early elementary education, and 20
different models are being implemented in Follow Through sites across the
nation. (p. 83).
Fourteen education models (i.e., different treatments) were included in the FT Evaluation
(Stebbins et al., 1973), and these varied in the degree of classroom structure, basic skills,
and parental involvement. One such model was Direct Instruction (DI), sponsored by the
University of Oregon, College of Education. In the DI approach, behavioral methods were
used with highly structured teaching materials. Teachers worked with small groups of
students, and tests were frequently administered to assess children’s progress.
There were two cohorts of students from East Saint Louis, Illinois. Each consisted of a
treatment (FT) group receiving DI and Non-Follow Through comparison (NFT) group. One
cohort was assessed from grades 1-3 (n = 96, 45 for FT, NFT), the other from K-3 (n = 56,
21 for FT, NFT). (Note 32) These were the groups providing data for the Gersten et al.
(1988) study. Nationally, however, Direct Instruction was implemented at 9 other sites.
Outcome measures included the Metropolitan Achievement Test with subtest scores in
Word Knowledge, Spelling, Language, and Reading, among others. The NRP analysts
choose to compute effect sizes for Reading (d = .11, 28) and Spelling (d = ‑.12, .16) for the
two cohorts. The Reading effect size was classified as a measure of comprehension. The
effect sizes were quite close to calculations from the present study of (.09, 27) for Reading
and (‑.10, .15) for Spelling. Similar national-level estimates of .14 and .12 for Reading and
Spelling (for the K‑3 cohort only), respectively, were given by Camilli (1980).
Overall, the results from East Saint Louis are remarkably representative of the national
results, but since Direct Instruction was only 1 of 14 other models, we might ask which
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models showed the largest gains in Reading and Spelling. Camilli (1980) found that two
models with the largest Reading effect sizes were Language Development (d = .180) (Note
33; Note 34) and Interdependent Learning (d = .168) (Note 35). In Spelling, the Parent
Education (Note 36) (d = .310) and Cultural Linguistic (.341) (Note 37) models had the
largest gains. We would add that the Direct Instruction model had the largest gain for MAT
Language, Part B (d = .327), in which a student was required to recognize asking, telling,
and incomplete sentences.
In conclusion, our statistical results are close, in this case, to those of the NRP analysts.
Thus, our extended analysis of the Gersten et al. (1988) study can be taken as validation of
the consistency of their methodology. However, this case study points to other aspects of the
NRP study in terms of its generalizability, or external validity. It is ironic that a single study
can strengthen conclusions regarding the value of phonics instruction, and yet the study was
originally embedded in a larger study that provided mixed findings with regard to treatment
efficacy. Though it is true that the basic skills models (Direct Instruction and Behavior
Analysis) had the largest overall gains in the Follow Through experiment, the Direct
Instruction model did not outperform other models for Reading or Spelling.
Data from FT models other than Direct Instruction were not included in the phonics
instruction meta-analysis for several probable reasons. First, it is doubtful that reports such
as those by House et al. (1978) would be identified with the NRP key word searches. It
would be virtually impossible in a meta-analysis to anticipate such studies without direct
knowledge of their existence. Studies like Camilli (1980) (Note 38) or the FT evaluation
reports (e.g., Stebbins et al.., 1977) would not be included because they do not appear in
refereed journals. However, even if such studies were located and included, a dilemma
would arise because both the NFT and other FT models could serve as controls. Only if
enough information were reported for comparing the level of phonics instruction in the
alternative treatments could a consistent decision be made. This might be possible even
though the data are about 30 years old, but such an in-depth analysis would not be
Tunmer, W. E., & Hoover, W. A. (1993)
This study compared the effects of three different language programs on beginning readers
who had been identified as having reading difficulties. Two types of Reading Recovery
programs were used for the treatment groups, and the standard intervention program was
used for the control.
The first treatment group was the Standard Reading Recovery (SRR) program, which is a
remedial reading program developed in New Zealand to “reduce the number of children with
reading and writing difficulties.” At risk children were selected and provided with 30-40
minutes per day of individual instruction by a trained teacher for a period of 12-20 weeks.
Reading Recovery lessons followed the procedures developed by Clay (1985) and usually
included seven activities, one of which was writing a story the child had created. Writing
exercises employed phonological awareness training techniques to isolate individual sounds
in familiar printed words. Incidental word analysis activities that arose from the children’s
responses were available after the children mastered letter identification. This instruction
was given in addition to the children’s regular classroom activities.
The second treatment group was the Modified Reading Recovery (MRR) program. It held
the parameters of the standard program constant and then added explicit and systematic
46 of 51
instruction in phonological recoding skills to the letter identification activities of the
standard Reading Recovery program. The control group was the Standard Intervention
Group. It received support services that were normally available to at risk readers, mostly
funded by the (then) Chapter 1 program. Children were instructed in small groups, and
instructional techniques varied greatly and included word analysis activities.
First graders with mean age of 6 years 2 months at the beginning of the school year were
drawn from a pool of at risk readers from 30 schools across 13 school districts. The lowest
ranked children from each school were given the Diagnostic Survey and Dolch Word
Recognition tests. Three matched groups were formed from those who performed at the
lowest levels on these tests. The 64 children in the two Reading Recovery treatment groups
were drawn from 34 classrooms from 23 schools. The control group of 32 students was
drawn from 13 classrooms in 7 schools. Classrooms were “roughly” matched on location,
SES and type of classroom reading program. No significant differences were observed
between the means of the three comparison groups for age and all pre-treatment measures.
The study also reports that two additional control groups of 32 children each were added (p.
170), but there is no further mention of these latter groups.
For this study, the NRP analysts choose two groups, the MRR group and the Standard
Intervention group. Effect sizes were then computed for 4 outcome categories: Word ID (d =
2.94), Spelling (d = 1.63), Nonwords (d = 1.49), and Oral Reading (d = 8.79). These effect
sizes, especially the latter, seem very large, and this could be taken to mean that the effects
of systematic phonics instruction were quite impressive. However, it should be noted that
systematic phonics instruction was the key element in the MRR group that distinguished it
from SRR. By comparing these two groups, we can obtain an estimate of how much
improvement resulted from this modification to the standard program. We calculated these
effect sizes as Word ID (d = -.12), Spelling (d = -.25), Nonwords (d = -.12), and Oral
Reading (d = .12). These results indicate that these two groups performed at very similar
The large SRR effect sizes may be due to either the size of the treatment unit or the RR
treatment itself, but these two factors are completely confounded in this study. While the
children in both Modified and Standard Reading Recovery groups received one-to-one
tutoring, the children in the Standard Intervention group received small group treatment. In
fact, the authors warned that
It is important to note, however, that the highly significant results in favor of the
two Reading Recovery groups over the standard intervention may not have been
due to the Reading Recovery program per se (i.e., the diagnostic procedures, the
format of the Reading Recovery lessons, the procedures for discontinuation) but
rather to the manner in which the instruction was delivered. Reading Recovery
involved one-to-one instruction, whereas the standard intervention involved
instruction in small groups. (pp. 172-173)
It is arguable, in fact, that taking the authors’ wisdom into account would result in an effect
size for Oral Reading of d = .12 in contrast the NRP estimate of d = 8.79. Once again, we
see that there is a significant issue involved in determining the definition of “control group.”
Whereas the NRP guidelines clearly designate the standard intervention as having the least
systematic phonics instruction, it is the comparison of the MRR and SRR groups that is
most germane to estimating the systematic phonics effect (in our study represented as the
47 of 51
Foorman, B., Francis, D., Novy, D. & Liberman, D. (1991)
This study explored the relationship among phonemic segmentation, word reading and
spelling, with the intention of demonstrating the superiority of a more letter-sound (labeled
“More-LS”) approach of reading instruction. Children receiving less letter-sound instruction
(labeled “Less-LS”) were not expected to exhibit regularity effects in word reading to the
same extent or at the same rate as children receiving More-LS instruction.
Two groups were selected to participate in this study. The Less-LS group was comprised of
40 students enrolled in three first grade classrooms in a Houston, Texas, public school. The
More-LS group was comprised of 40 students in three first grade classrooms in two Houston
parochial schools. Students in all six classes received one hour of reading instruction daily,
and both groups used a basal reading series. Children enrolled in the parochial schools were
younger by about 2 months on average (p < .05); and they had higher initial reading and
PPVT (Peabody Picture Vocabulary) scores, though the latter differences were not
significant. Public school classes had, on average, a PPVT standard deviation about 60%
larger than that of parochial school classes.
Neither the treatment nor the control regimen was designed or manipulated by the
researchers; both reflected the regular teaching habits of the individual classroom teachers.
Teachers in the three public school classrooms were described as being committed to
“dealing with whole words in meaningful contexts,” and described themselves as using a
“language experience” strategy to teach reading. The Less-LS teachers used daily story
selections from the basal series Harcourt Brace Jovanovitch Reading to provide a theme
around which instruction was based. Teachers in the three parochial school classrooms were
described as being “committed to letter-sound correspondences and having children segment
and blend sounds in isolation.” (p. 458). Rules for relating letters and sounds, and sequenced
spelling patterns were taught using Scott, Forseman Reading, Phonics Practice Readers,
Series B and Modern Curriculum Press Phonic Program (a workbook). Approximately 45
of the 60 minutes devoted to reading instruction were spent on letter-sound activities. A
Scott Forseman basal reading series was also used.
The study was approximately ten months in duration. Students were administered pre-test
measures in October of first grade, with post-test measures administered the following
February and May. The following tests were administered: Gates-MacGinitie Reading Test,
Basic R, Form 1; Peabody Picture Vocabulary Test – Revised, Form L; a spelling test
(researcher-made test consisting of 40 regular and 20 exception words), a word reading test
(researcher-made test consisting of 40 regular and 20 exception words); and the 13 item Test
of Auditory Analysis Skills, TAAS. There were no significant posttest group differences in
TAAS mean scores or trends. There were significant differences in trends of spelling scores
(both regular and exception words) and trends of word reading scores (both regular and
exception words) favoring the more LS-group. In other words, the more LS-group appeared
to improve at a faster rate than the Less-LS group in word reading and spelling.
For the three primary outcome variables (Word Reading, Spelling and TAAS), the
researchers did not report standard deviations. In this instance, it appears that the NRP
analysts used the simple standard deviation (for the effect size denominator) of class means.
According to standard statistical theory, this results in an effect size that is too large by a
factor of √n, where n is the number of students in the classes. The NRP effect sizes for Word
ID (d = 1.92), Decoding (d = 1.67), and Spelling (d = 2.21) are not comparable to those of
48 of 51
other studies in which the individual student is the basis for standard deviation calculations.
In this case, we converted the effect size to the individual student metric and obtain the
following: Word ID (d = .48), Decoding (.62), and Spelling (.49). On average, the effect
sizes are 3-4 times smaller than those computed by the NRP analysts, which reflect class
sizes of about 13 (for participating subjects). Moreover, approximate matching does not
completely resolve the issue of what portion of the adjusted ds should be attributed to
treatment, school type (public versus parochial), and school-by-treatment interaction.
In conclusion, the Foorman study for the most part succeeded at controlling initial
differences. However, there is some evidence to suggest that the public school students
lagged slightly behind their parochial school counterparts, and that individual differences in
ability (PPVT-R) were somewhat larger in the public school classrooms. (Note 39)
We do not know the degree to which this initial difference may have affected posttest
differences or rates of growth. However, it is clear that the effect sizes need to be adjusted to
the individual student metric.
Vickery, K.S., Reynolds, V.A., & Cochran, S.W. (1987). Multisensory
teaching approach for reading, spelling, and handwriting,
Orton-Gillingham based curriculum, in a public school setting. Annals of
Dyslexia, 37, 189-200.
The study reports the results of a four-year study (1978 – 1981) that investigated the effect
of the Multisensory Teaching Approach for Reading, Spelling and Handwriting (MTARSH)
in both remedial and nonremedial classes in a public school. The study reports the result of
California Achievement Test, which were administered annually in April of each year. The
MTARSH was developed by adapting the individualized Orton–Gillingham-Stillman
method to small homogenous groups of students. The MTARSH employs two basic
decoding techniques, synthesizing phonics and memorizing whole words.
The authors report the baseline scores for each grade and the posttest scores of both remedial
and nonremedial classes (separately) taken after 1,2, 3 and 4 years MTARSH instruction.
The remedial classes were composed of students who qualified for Chapter 1 or special
Education/LLD program, at risk of presenting reading difficulties. All other children
enrolled in this school were classified as non-remedial. The MTARSH Program was
employed for all students, both remedial and non-remedial, in this school (n = 426 during
the four years covered by this study). The amount of instruction received is equal for both
groups- 25-minutes per day for the first graders and 55 minutes of daily instruction for
grades 2 through 6. For the remedial classes, MTARSH program was their only instruction
in reading, spelling, and cursive writing. The non-remedial classes MTARSH program was
taught in lieu of the regular state-adopted spelling and handwriting programs, using the
supplemental reading materials and the basal readers. Although detailed instructional
method and materials were different in two groups, the MTARSH method used in both
classes was treated as comparable in this study.
The baseline score is from the pre-tests administered two years prior to the introduction of
the MTARSH program. The intervention effect was measured by the difference between the
49 of 51
baseline scores and the posttest scores. The analysis was conducted separately for remedial
group and nonremedial groups. The NRP reports eight effect sizes for this study under
general reading category. (Alphabetics, Part II. Appendix G. page: 2-174). Effect sizes are
reported for 3rd 4th, 5th and 6th grades for both remedial and non-remedial groups, which
yielded the 8 effect sizes computed by the NRP team. Through recalculation of the effect
sizes using the formula reported (NRP Report, page 1-10) and the sample sizes reported in
Appendix G, it was verified that the NRP used baseline averages as the “control group”
outcome, and the one-year follow-up test averages as the “experimental” outcome. The
effect sizes were reported to represent the magnitude of performance differences between
the phonic instruction (Orton–Gillingham method) and regular class instruction that was
provided before the MTARSH was instituted. This study examined the effect of one
instructional method on two different populations; no control group, or other instructional
method, was available for comparison. The design is clearly pre-post and does not satisfy a
strict interpretation of the quasi-experimental requirement for inclusion (NRP, pp. 1-7 to
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Universidad Autónoma de Puebla
María Beatriz Luce(Brazil)
Universidad Federal de Rio Grande do
Javier Mendoza Rojas (México)
Universidad Nacional Autónoma de
Marcela Mollis (Argentina)
Universidad de Buenos Aires
Humberto Muñoz García (México)
Universidad Nacional Autónoma de
Angel Ignacio Pérez Gómez (Spain)
Universidad de Málaga
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Simon Schwartzman (Brazil)
American Institutes for Resesarch–Brazil
Jurjo Torres Santomé (Spain)
Universidad de A Coruña
Carlos Alberto Torres (U.S.A.)
University of California, Los Angeles