Mehta (1998) by Taylor, Anderson, Au, and Raphael (2000). The major finding of Foorman et al. (1998) was an advantage for reading instructional approaches that emphasized explicit instruction in the alphabetic principle for at-risk children. This finding is consistent with a large body of research over the last 30 years, much of which has been funded by the National Institute of Child Health and Human Development (NICHD; Fletcher & Lyon, 1998; Pressley, 1998). Stanovich (1998) puts our study—referred to below as the Houston study—in perspective in his award address to the National Reading Conference:

…The current scientific consensus is that direct instruction in alphabetic coding facilitates early reading acquisition, especially among disadvantaged children. The Houston study, when finally integrated and interpreted – with the hundreds of other relevant studies (the hundreds of studies synthesized in the review papers published above) – will either strengthen the moderate-strong consensus in the direction of strong, or weaken it a bit in the direction of moderate. …Critics of this study are acting as if we are at some neutral balance point and that this study is going to tip things definitively in one direction or another. This is a mischaracterization of the literature – and of science. The flailing and uninformed critiques of this study by whole language advocates have badly missed the mark and are embarrassing in what they reveal about the critics’ grounding in the logic and evolution of scientific knowledge.

In the abstract of their article, Taylor et al. (2000) criticized us for a "simple solution to the complex problem of raising the literacy of young children in high poverty neighborhoods." We have never maintained that a single solution exists to this problem, let alone a “simple solution.” However, we do maintain that there are some instructional principles that teachers and schools can use to enhance the reading achievement of at-risk children, and that it makes sense to demonstrate effective implementation of these instructional principles before investing in more complex solutions. They also stated in the abstract that “Researchers investigating beginning reading should exercise extra caution to delimit findings from their own studies.” We agree with this, which is why our discussion section cited nine specific limitations of the study and we have systematically responded to Taylor et al. (2000), Coles (2000), and other misrepresentations of the research in journals, the media, and policy organizations. No single study should be the basis for public policy. As Stanovich indicates, there is a large body of research that supports the conclusions in Foorman et al. (1998).

Taylor et al. (2000) attributed four assumptions to our research: (a) word level processing equals reading, (b) cultural difference equals deprivation, (c) instructional method equals teaching, and (d) training equals professional development. Their article in the Educational Researcher and a nearly identical report posted on the CIERA website (http://www.ciera.org) during the Fall, 1999, purported to examine how these assumptions shaped our analyses and prohibited us from considering alternate interpretations of the data, based on their analysis of the text of the article and the context around the attention to the article.

Taylor et al. (2000) acknowledge “Barbara Foorman and David Francis for patiently answering a number of questions, providing further information about the study, allowing us to examine the word reading test, and describing additional analyses of the data.” But hardly any of our responses are reflected in the published critique. Because of our repeated, yet thwarted, attempts to correct researchers’ misunderstandings, we have entitled this response “Misrepresentation of Research by Other Researchers.” If we had room for a subtitle it would be: “Why Aren’t Researchers Using their Time to Replicate Research or to Generate New Research to Address Pressing Questions about how Children Learn to Read?”.

Our response is organized into six sections. First, we provide a brief overview of the most important findings from the Foorman et al. (1998) study. This is necessary because many seem content with media or detractor reviews of the study, which reduce it to a program evaluation comparison of phonics vs. whole language reading methods. Foorman et al. (1998) is a study of instructional principles in relationship to child characteristics, not a program evaluation study. Second, we correct the fiction regarding pre-publication history. Third, we address the criticism that we equate reading with reading words. Fourth, we respond to the claim that we are insensitive to cultural differences, to teachers, and to professional development. Fifth, we address the concern that investigators’ lenses can constrain interpretation by identifying the mistakes Taylor et al. (2000) make in the reanalysis of our findings. Finally, we address policy issues by inviting our critics to join us in tackling pressing research questions in reading.

Overview of Foorman et al. (1998)

The research questions addressed in Foorman et al. (1998) were: (a) the degree of explicitness of alphabetic instruction required by children at risk for reading failure and (b) the extent to which the reading development of such children depends on their growth in phonological processing skills. The three classroom approaches studied represented three currently prominent and distinct views on the explicitness of alphabetic instruction in order to develop beginners’ phonics and decoding skills within a print-rich environment. One approach emphasized explicit instruction in letter-sound correspondences practiced in decodable text (direct code; DC). Another approach emphasized less explicit instruction in systematic sound-spelling patterns embedded in connected text (embedded code; EC). The third approach emphasized implicit instruction in the alphabetic code while reading connected text (implicit code; IC-Research). We also included teachers using the district’s standard classroom instruction of implicit code (IC-Standard) as a comparison of the effects of staff development. This group was included as a comparison for the IC-R group. Comparisons of the IC-R group with the EC and DC groups are not warranted because these groups differed from IC-S in terms of the approach to instruction as well as the support and professional development provided to the teachers. The instructional approach of the tutorial sessions was either matched to one of the three classroom approaches or involved the district's standard tutorial regimen based on the work of Clay (1991).

This research was carried out in a school district that was a model for whole-language instruction, using techniques outlined in Routman (1991) and Weaver (1994). No basal was employed and no explicit ordering of phonic elements was used. The emphasis was on the construction of meaning through authentic literature and the integration of reading, spelling, and writing into literacy activities that provide a context for phonics. Participants were 375 Title 1-served first and second graders and 66 volunteer classroom and Title 1 teachers in 8 of the 19 elementary schools in that district in metropolitan Houston (Foorman, Francis, Beeler, Winikates, & Fletcher, 1997). The percentage of the school populations receiving free or reduced lunch ranged from 32% to 64% in the seven schools with IC-R, EC, and DC instruction. The school with IC-S instruction had 71% of students participating in the free or reduced lunch program. As we clearly stated, this difference limited the inferences that could be drawn from comparison of the IC-R and IC-S groups, but has no bearing on the comparisons among IC-R, DC, and EC, a point that appears to have been lost on D. Taylor (1998) and in Coles (2000). School effects in the experimental instructional approaches (i.e., IC-R, EC, and DC) were controlled by having at least two instructional approaches in three of the schools. Foorman et al. (1998) reported on 285 children and 53 classroom teachers, dropping 90 children who did not receive tutoring so that a completely nested analysis of child within teacher would be possible without any missing cells in the crossing of instructional approach with tutorial.

The Embedded Code approach was a classroom adaptation of Hiebert, Colt, Catto, and Gary (1992). A list of spelling patterns and materials was obtained from the St. Vrain Valley School District in Colorado where this program had been implemented. Reading instruction in EC classrooms took place in trade books rather than a basal, as in the IC classrooms. However, the use of an ordered list of spelling patterns made EC instruction much more systematic than IC instruction. Classrooms following the direct code approach used the basal reading program, Collections for Young Scholars (Open Court, 1995), which emphasizes a balance of skill- and literature-based activities. In terms of phonics, the first 30 lessons are devoted to phonemic awareness and an understanding of the alphabetic principle; across the middle weeks of the program, 42 spelling-sound correspondences and spelling conventions are explicitly taught and exercised using sound-spelling cards, alliterative stories, blending activities, and controlled vocabulary stories for practicing newly taught patterns in context. More detailed descriptions of these instructional approaches are provided in Foorman et al. (1998) and in Snow, Burns, and Griffin (1998, pp. 199-206).

Professional development for the participating teachers consisted of one week of curriculum-specific and generic strategy instruction during the summer, frequent within school meetings, and three meetings across schools of teachers involved in IC-R, DC, and EC instruction. IC-S teachers participated in the district’s usual staff development. Research staff and teachers agreed on the components of each instructional approach (i.e., IC-R, EC, and DC), and these components became the basis of a checklist that researchers used when observing classrooms. In addition to completing these monthly checklists, researchers also copied lesson plans, and asked teachers to complete a survey at the end of the year regarding their satisfaction with their instructional program. There were no differences in the amount of staff development provided to the three research conditions.

This quasi-experiment was designed in such a way as to produce inferences that were as valid as possible given several constraints. First, we wanted the study to be conducted using real classroom teachers. Second, we intended a comparison of instructional principles embedded in curriculums commonly employed with children eligible for Title I services in order to ascertain the extent to which different instructional principles can mitigate against poor academic outcomes characteristic of this population. The third and final constraint was that random assignment of teachers and students to classroom and conditions was not possible. It is important when discussing or criticizing the study to keep the above constraints in mind, and to recognize the controls that were built into the study in order to provide the strongest possible basis for drawing valid inferences from this quasi-experiment. The key controls built into the study were: a) the placement of multiple instructional approaches within a single school, b) the providing of professional development to all teachers delivering the three instructional programs of interest, c) inclusion of a district standard comparison school as a comparison for the impact of professional development in the IC-R group, and d) allowing teachers to self-select programs in order to ensure high motivation and to limit diffusion. Finally, the study was designed to be longitudinal within a given academic year with more than two waves of data collection (Rogosa, 1995) to avoid problems of regression to the mean.

In designing the assessment schedule and battery, serial as well as single time point assessments were included in order to rule out differential practice effects as the basis for group differences that emerge over time in the serial assessments (Foorman et al., 1999). Moreover, we assessed a range of academic skills chosen to reflect a gradient of generalizability to the effects of the different instructional approaches. Specifically, students were assessed four times a year to measure growth in vocabulary, phonological awareness (PA), and word-reading skills, along with other measures not reported because they did not alter the interpretation of the results (space in journals is not given for redundant reporting). At the end of the year we individually administered standardized intellectual assessments and tests of reading and spelling. Additionally, we collected school attendance data and measures of self-esteem, reading attitudes and experience, behavior, and environmental information in the spring (see Foorman et al., 1998, for detailed descriptions of these measures).

Given these measures and the instructional programs under investigation, it would be expected that the effects of DC would be strongest on measures of PA, next strongest on measures of word reading, and weakest on measures of comprehension and vocabulary. This gradient of generalizability is hypothesized under DC because the instruction targets the development of PA, which enables students to improve decoding skills. Through the development of word reading skills, children develop the ability to read and understand text. That is, the DC approach is based on a model of reading that has PA mediating the development of word reading skill and word reading skill mediating the development of comprehension skills. Vocabulary development occurs through the practice of skilled reading. In contrast, effects of IC would be strongest on comprehension and vocabulary, weaker on measures of word reading and weakest on measures of PA. EC would be expected to have strongest effects on spelling and word reading, weaker on PA, and weakest effects on comprehension and vocabulary. The IC and EC approaches target different proximal (EC – recognition of orthographic patterns) or distal (IC – extraction of meaning) skills and, consequently, would be expected to show their largest impact in areas different from DC if, in fact, the instructional principles in these approaches were most effective. To the extent that non-random assignment simply placed the best teachers or the brightest of the disadvantaged students in one type of instructional condition, we would not expect instructional effects to follow this gradient of generalizability, but rather to reflect a general superiority of one approach across all measured domains. This general superiority would be expected to be apparent at the beginning of the year, and to be relatively consistent in magnitude across domains, or at least not expected to follow one of the predicted gradients of generalizability.

As the reader can readily verify in Foorman et al. (1998), instructional effects tended to follow the gradient of generalizability that was consistent with an effect of DC instruction. Controlling for differences in age, ethnicity, and verbal IQ, we found that children in the direct code (DC) approach improved in word reading at a faster rate and had higher word recognition skills in April than children receiving the implicit code (IC) approach (either the research-based IC or the district’s standard IC). More importantly, children in all instructional groups with higher phonological processing scores in the beginning of the year demonstrated improvement in word reading skills across the year. However, because children with low initial status in phonological processing were more likely to improve in word reading if they received explicit instruction in the alphabetic principle than less explicit or implicit instruction, we feel that it was the components of the program that explained the different patterns of results. One would expect initial phonological awareness to be less related to outcome in DC classrooms because DC provides more explicit instruction in the alphabetic code, and more explicit instruction is more effective in developing phonological processing skills in all children. The effect of explicit instruction on development of phonological processing thereby minimizes the importance of the initial level of this skill that children bring to the classroom in the fall (see pp. 25-26 for a more detailed discussion). We are pursuing this important finding by comparing the DC program used in this study (i.e., Open Court, 1995) with other DC programs that vary in the degree of scriptedness of the teacher’s guide and in the degree of decodability of connected text.

In summary, the results of this study support other research findings showing that instructional approach makes a difference for the development and outcomes of reading skills in first and second grade children at-risk for reading failure (Foorman, 1995; Snow et al., 1998). However, not all instructional approaches were equal. At-risk children whose program included explicit instruction in the alphabetic principle improved at a significantly faster rate than children indirectly instructed. At-risk children whose instruction was at an intermediate level of explicitness – the EC approach – were at an intermediate level of reading growth and outcomes. Group differences in reading comprehension paralleled those for word recognition, but were less robust. Effect sizes were in the moderate to large range and the overall effect was statistically significant. Additionally, these performance differences were due to instruction and not to behavioral or affective differences among groups. Similarly, although outcomes varied across classrooms, measured characteristics of the teachers did not relate significantly to outcome. Generally, teacher’s attitudes toward and implementation of instructional practices were very good across instructional groups and the amount of time devoted to reading and language arts was comparable.

That more explicit instruction in the alphabetic principle had the effect of leveling the playing field for children who start school low in phonological processing suggests a number of important lines of research on how best to balance instructional time across activities at various points in children’s early school experience. Questions of this type are being actively pursued by us as well as other educational researchers, and would benefit from further examination from other research perspectives. However, reluctance to accept the basic finding, supported by a broad body of research, on the benefits of explicit instruction in the alphabetic principle for at-risk children has precluded pursuit of these questions by the full complement of educational research perspectives. This current state of affairs is regrettable and limits advancement of the field.

Pre-Publication History of Foorman et al. (1998)

It is ironic that Taylor et al. (2000) would criticize us for presenting results prior to publication when their critique was posted on a public website several months before publication. We also note that some members of Taylor et al. (2000) discussed their critique with a reporter long before we were aware of its existence. The reporter believed a scandal had been unearthed, but eventually decided there was nothing to write about. In fact, the results of the Foorman et al. study were presented at two invited symposia prior to publication. In retrospect, the order of events may appear unfortunate. But the reality is that in virtually all areas of research, including education, presentation prior to publication is the norm.

The first presentation was at the Learning Disabilities Association (LDA) meeting in Washington, D.C. in March 1996 and was explicitly organized so that reading researchers funded by the NICHD could present preliminary results. Researchers may not like to share preliminary results, but the fact is that yearly progress reports for any federally funded projects are a matter of public record. The LDA published the papers from the symposium in their journal 10 months later (Foorman et al., 1997). Hence, the Taylor et al. (2000) claim that we described results to Education Week (Manzo, 1997) prior to publication is incorrect. Furthermore, the Taylor et al. claim that we highlighted findings in the 1997 publication that were “not deemed sound enough for ultimate publication” in the 1998 publication in the Journal of Educational Psychology is also not correct. To reiterate, in the analyses in the original submission to the Journal of Educational Psychology a sample of 375 children was used. This sample included 90 students who were eligible for Title 1 services based on the district’s informal assessment, but who were not served due to the schools’ decisions on how to allocate spending of their Title I funds. The important point is that the pattern of results was the same whether these untutored students were included or not included. At the suggestion of one of our reviewers, we reanalyzed the data excluding these students because they confounded our analysis of the effects of two different kinds of tutoring at two different ratios. By analyzing the data only from those students who actually received Title 1 services, we were able to nest tutored students within classroom instruction in the analysis and control total time spent in reading instruction as classroom time plus time in tutoring. The manuscript was resubmitted to the journal based on the reanalysis to address the reviewers’ comments and was ultimately accepted for publication in that form.

In attendance at the LDA meeting in March 1996 was Marion Joseph, who is now a member of the state board of education in California. Mrs. Joseph told Steve Baldwin, chair of the educational subcommittee of the California legislature about results presented at the LDA symposium. Drs. Lyon and Foorman were asked to testify before the education subcommittee in May 1996, one year after California had passed its ABC bill. Researchers funded by the government are obligated to respond to explicit requests of this sort. Videotapes of these testimonies reveal typical academic accounts of research findings rather than the sensational, conspiracy-motivated fiction in D. Taylor (1998). However, most media accounts of our testimony and of Foorman’s invited presentation at the American Association for the Advancement of Science (AAAS) meeting in Seattle, Washington February 16, 1997, were problematic because our four-group comparison of IC-S, IC-R, EC, and DC became reduced to a two-group comparison of Whole-language versus Phonics. On February 19, 1997, The Globe and Mail published a front page article describing our study presented at AAAS as simply a phonics versus whole-language comparison where phonics won. On February 18, 1997, the London Times published a fairly accurate description of our four-way comparison presented at AAAS. If the two articles were lined up next to each other it would be difficult to guess that they were describing the same study. On March 3, 1997, researchers at the University of Toronto (Booth, Dudley-Martin, Murphy, & Wells, 1997) wrote a commentary to The Globe and Mail complaining about our lack of attention to comprehension. We wrote a response on March 10, 1997 (Foorman, Francis, & Fletcher, 1997), explaining that the design included four, not two groups and that the large effect size of the comprehension results was of practical importance. In spite of our clarification, some members of the board of the International Reading Association talked the editor of the IRA’s newspaper, Reading Today, into republishing the Wells et al. commentary. Thus, the misrepresentation of our study by the media became instantiated in the minds of reading educators across the nation. We were successful in convincing the editor of Reading Today to reprint our rebuttal to Booth et al., but we were not successful in convincing him to reprint the London Times and The Globe and Mail articles side by side so as to show how the media can distort information.

In contrast to the implications of Taylor et al. (2000), we have responded in writing and by personal communication to numerous misrepresentations of our research by the media, by policy-oriented organizations, and by reading professionals. For example, in the spirit of the freedom of information act, we sent Gerry Coles a disk containing our data. Coles proceeded to selectively drop classrooms in our dataset so that he could write his essay. Education Week gave Coles prime-time space and cute reading-wars graphics to advertise his new work of fiction (Coles, 1999). We sent a rebuttal to Education Week that included a table of the actual classroom means of the comprehension data and explained how Coles had recomputed IC-R and DC classrooms means to fit his story. Education Week limited us to a 500-word response, so we alerted the readers to the misrepresentation of our data and provided our website address where the table of classroom means and an explanation of Coles’ apparently inappropriate manipulations could be found (Foorman, 1999a). He declined our offer of assistance in the interpretation of the data and refused to share his analyses with us prior to or after publication of his book (Coles, 2000). Thus, the misrepresentation was perpetuated by Coles and the media.

We have responded to other critiques of our study, in publications (Foorman, 1999b; Foorman, Fletcher, & Francis, 1999) and in letters to Denny Taylor, Gerry Coles, and Dianne McGuiness, which were published and posted on our website (http://cars.uth.tmc.edu) for review by others. Dianne McGuiness’ critique of our study, published in ParenTeacher Magazine (April, 1998) and posted on their website (http://www.ReadAmerica.net) is particularly relevant because she criticized us for not doing small, tightly controlled experimental studies. Yet D. Taylor (1998) and B. Taylor et al. (2000) criticize us for being too experimental and not sufficiently sensitive to cultural context. What we find curious is how seldom our responses to criticism prior to their publication show up in the final publication.

Who Believes that Reading is Simply a Matter of Reading Words?

We define reading as the process of deriving meaning from printed material. We further assume that this complex human behavior hinges on many component behaviors. These component behaviors include the identification of the individual words that comprise the text and the activation of the specific meanings of these words as relevant to the context in which the words are currently being presented. There is a robust body of literature that demonstrates conclusively that children understand text better when they are able to recognize the words that make up the text, and that understanding is further enhanced when recognition is automatic and effortless (see reviews in Adams, 1990; Rayner & Pollatsek, 1994; Snow et al., 1998). A substantial portion of this literature further demonstrates the high correlation between the ability to recognize words out of context and the ability to understand text presented in context. Thus, while reading word lists is not “reading,” reading words in lists measures one of the many important skills that children employ when reading connected text, and as such is an important skill to measure in a study of early reading development. If one only measures the ability to construct meaning from text, then if students fail in understanding what they have read, one cannot determine the basis for this failure. Is comprehension poor due to failure to recognize the words, limitations in vocabulary, or lack of automaticity in word recognition? Because comprehension is multi-determined, we measure the component skills of word recognition, automaticity, and vocabulary, in addition to measuring comprehension.

We know of no researcher who believes that reading equates with reading words. Concluding that the ability to read words is an important, or even necessary component of literacy development, does not mean that it is sufficient. Taylor et al. (2000) state: “CIERA emphasizes the importance of well balanced instructional programs that benefit all children who are learning to read.” We agree with this statement, as well as the following: “…understanding the alphabetic principle…is but one of many factors that need to be addressed to improve the reading achievement of young children in urban schools.” Alphabetic understanding (including phonemic awareness), reading fluency, and comprehension exist within a set of necessary but not sufficient conditions that are themselves nested within home, school, and community contexts. By the same token, as we explained to D. Taylor, “We do not assume that training children to read words and pseudowords will enable them to read cohesive text. What we do claim is that children who are unable to read words and pseudowords will not be able to read text at age level. “ We also claim – like many others (e.g., Stanovich & Siegel, 1994 for a review) – that the proximal cause of reading failure most commonly occurs at the level of the single word. Given this context, which apparently departs from the perspective endorsed by B. Taylor et al. (2000), we reject the notion that “The text provided by Foorman and her colleagues focuses unduly on instruction in word level processing as the key to beginning reading” (p.4). Their analysis is subjective, reflects their own biases, ignores compelling amounts of data, and ignores other papers we have written that discuss the need for balance in early reading instruction (Foorman, Fletcher, & Francis, 1998; Foorman et al., 1999).

Taylor et al. (2000) are critical of our word reading list and our lack of authentic text reading measures. With respect to our experimental word-reading list, they claim that it was too difficult. We had provided them results of our Item Response Theory analysis of the word list to show the item difficulty parameters. Because the list had been developed in a non-Title 1 population, we acknowledged that the Grade 1 list would benefit from some lower-level items (which we had added). However, we pointed out that there were easier items on the Woodcock-Johnson Letter-Word Identification subtest (Woodcock & Johnson, 1989) at the end of the year and the same pattern of results emerged. They also argue that we should have included easier words that students might have encountered in instruction. If we had done this, then we would not know if the differences between groups on the outcome measures simply reflected greater exposure to those instructed words in one or more of the instructional groups. Instructional materials varied across condition, and we attempted to ensure that the words on the list were not more likely to be used in one condition than another. Furthermore, Taylor et al. (2000) argue that the effect we observed might be due to students in DC having more opportunity to decode hard words, but they offer as a solution the use of high frequency words that students might have encountered in instruction. If we had done that and found an advantage for DC, wouldn’t it be reasonable to argue that the DC students had more exposure to those words in instruction?More generally, not only did Taylor et al. (2000) ignore our factual presentation of difficulty parameters and the illogic of their recommendations, they accused us of exploiting poor children: "Exploiting these comparisons in their zeal to prove their theory, Foorman and her colleagues have the effect, no doubt unintended, of shaming poor children and their teachers...They create the unfair and ultimately dangerous impression, whatever their intentions, that reading instruction in a number of urban public classrooms is worthless." (p. 7) We wonder who is shaming whom. Taylor et al.’s (2000) low expectation of Title 1 children produces a self-fulfilling prophecy (Goldenberg & Gallimore, 1995). Expect little and you receive little! Our results clearly showed the floor is lifted for Title 1 children with low initial phonological awareness skills if explicit alphabetic instruction within a balanced approach to reading is provided. The fact that good instruction takes at-risk readers towards national averages in word reading and comprehension is something to celebrate, not to denigrate. Clearly, the word list was too difficult for many children, but that cannot explain why the word list was not too difficult for children in the DC classrooms. Moreover, the difficulty of the experimental word list cannot explain the parallel effects that were seen on the standardized reading measure at the end of the year. Finally, it is critical to bear in mind that the experimental word list was developed and normed on a sample (n=945) of children from the same school district attended by the Foorman et al. (1998) sample of Title I children (see Foorman, Francis, Fletcher, & Lynn, 1996).

In Texas, these Title I students will be tested on the same state-wide academic accountability measure as all other children attending public elementary school in Texas. The passing standard for these children on the state’s accountability measure is the same as for non-Title I children, and their schools are accountable for these student being able to meet that passing standard. While the difficulty of the experimental word list may mask some of the raw gains made by children who scored at the floor of the test, this masking applies to students in all instructional groups and cannot explain the differences among instructional approaches. In short, test difficulty cannot explain away the relative differences among instructional conditions, although inferences about absolute gains made by any one group must take test difficulty into account. Our statements about absolute gains should not be misconstrued to imply that children gained no skill. At the same time, the limited gains of some children are cause for concern. The longitudinal research that we have done with this word list shows quite strongly that children who are not reading words from the list by the end of first grade are at substantial risk for reading below grade level by the end of second grade. Thus, while Taylor et al. (2000) decry the unintended implications of our statements, we are more concerned that teachers, parents, and administrators understand that the gains seen for many children, especially in the IC-R and EC groups, were not sufficient to ensure that these children would be reading on grade level by the end of grade 2. This fact is not something to be ashamed of so much as it should be a call for action to improve the reading outcomes of those children. To ignore the information and simply hope for the best for these children, on the other hand, is shameful.

The criticism of our lack of a measure of real-world connected text is a criticism of the field, not of Foorman et al. Where is the data that says that one approach to assessing reading comprehension is better than another? From a construct validity perspective, there is no latent construct called “comprehension of authentic text”. Moreover, there is no simple measure involving authentic text to index the more broadly defined latent trait of comprehension. If there were, we would be the first to use it. When assessing reading comprehension, it is assumed that there is at least one “pure” construct that involves comprehension of written language. We are aware of no research, including our own (Fletcher et al., 1996), that shows there is more than one latent variable of reading comprehension, but this is an empirical question. Various formats for assessing reading comprehension are all imperfect indicators of the underlying construct. Some of the variance in any assessment reflects the actual construct, while other variance is measurement error or represents variance attributable to other constructs (e.g., word recognition). Thus, each of the formats for measuring the latent construct “reading comprehension” has its drawbacks. Story retelling or probed questions place demands on oral language skills and memory. Cloze procedures are disruptive to reading fluency. Running records are difficult to score reliably.

In an attempt to address the relations among different measures of reading comprehension and different reading contexts, we conducted a small study during our validation research on the Texas Primary Reading Inventory (TPRI; TEA, 1998; Foorman, Fletcher, & Francis, in press). In this study, 124 first graders were randomly assigned to read a story passage in the TPRI booklet, in the actual storybook, or in a guided reading context (McEnery, 1999). Each child read two short passages taken from children’s literature books, answered five comprehension questions, and retold the story they had just read. Reading rate and accuracy were recorded for each child for each passage. There were no differential effects of context on reading comprehension as measured by comprehension questions or retell scores. That is, reading a storybook passage printed in the TPRI booklet, versus reading the passage in the storybook with or without adult scaffolding, made no difference in the number of story grammar elements in first graders’ retells or number of comprehension questions answered correctly. For one passage—the one that was above a first-grade level—there were significant effects of fluency (i.e., reading rate) on answering comprehension questions and on retell scores. Specifically, speed and accuracy of decoding explained 13% of the variance in correctly answering comprehension questions and 10% of the variance in retelling scores. Moderate correlations were found among formal and informal measures of reading comprehension. Incidentally, half of the Title I first graders in McEnery (1999) (based on a different sample from Foorman et al., 1998) were not able to read simple authentic texts widely viewed as being appropriate for end of Grade 1 children. This compares with the 9% of children receiving DC instruction in Foorman et al. (1998) and 21-24% in the other conditions who could not read the material in the Formal Reading Inventory (Wiederholt, 1986). Clearly assessment of reading comprehension is an area that needs further research, and condemnations over selection of measures are premature.

Insensitivity to Cultural Differences, Teachers, and Professional Development

Taylor et al. (2000) claimed that we are insensitive to cultural differences, ignore differences attributable to poverty, and don't respect teachers. The assertion that we do not respect teachers is tacitly false, but stems from Taylor et al.’s (2000) own assumptions that teachers are equalizers of classroom instructional approaches. We believe this assumption can and should be empirically tested. To the extent that instructional approach affects achievement outcomes for any child, then to that extent lack of empirical knowledge about these effects and the contexts in which they occur leave to chance important aspects of that child’s academic environment, and therefore, their academic development. Saying that instructional approach matters for some children at certain points in their development in no way implies that instructional approach is all that matters, and most importantly should never be taken to imply that teachers do not matter. As we pointed out to Taylor et al. (2000) "the data in the paper indicate that the teachers (in all conditions) were enthusiastic about their instructional approaches, and this reflected the amount of professional development we provided as part of the project." In the past seven years we have conducted studies involving several hundred teachers, and we have yet to receive a single complaint from a participating teacher that suggested that the teacher felt that she or he was not respected or valued for their role in the education of their students. We agree with Taylor et al. (2000) that programs don’t teach, teachers do. But teachers have to teach something. What should that include? And is that not a legitimate question for educational research?

The failure of our responses to impact Taylor et al. (2000) makes their critique read like a projective test when we are said to come from a deprivation rather than a difference perspective, to equate instructional methods with teaching, and to equate training with professional development. Whatever one calls it—deprivation or difference—the amount and kind of literacy preparation children bring to school has direct implications with respect to what they need learn in school. With respect to the poverty issue, Taylor et al., like D. Taylor (1998), distort the facts. First, they describe the participating schools as high poverty schools, when in fact the range of free and reduced lunch percentages in the experimental schools is from 32.3% to 64.5%. This is the working poor, not the high poverty schools we have in our current NICHD early interventions project, with most schools above 90% on the free and reduced lunch program. Second, Taylor et al. talk about the supposedly large SES advantage in the DC classrooms compared to the EC classrooms. Yet they ignore the fact that the IC classrooms were in comparable or higher SES schools than the DC group, but still had the lowest achievement! Moreover, simple comparisons of schools are not meaningful because several of the schools used more than one instructional approach. Third, they take us to task for the higher percentage of African American students who were eligible for Title I in these schools. We did not qualify the students. They were qualified on the basis of their eligibility for the free lunch program and their poor reading as measured by the school district. They criticize us for not commenting on this situation. What would they like to see us say in our text about this situation? Rather than spend our time pontificating on and lamenting the conditions that allow this disproportionate representation to be the case (and it is not simply the case in this district, but in districts across the country), we are studying whether or not this situation can be addressed by improving instruction. Perhaps if all of these children had received direct, explicit instruction in the alphabetic principle as part of a balanced approach to early reading development in kindergarten, this disproportionate representation would not exist. Altogether, Taylor et al. (2000) have taken part of the puzzle and blown it out of proportion to fit their story. They attempt to weave a patchwork of explanations and limitations, each one different, and each one explaining a different effect in Foorman et al. (1998). At the same time, they ignore the fact that a simple explanation can account for virtually every effect, namely that children at-risk for reading failure due to low levels of phonemic awareness are benefitted by more explicit methods of reading instruction. While the factors that influence school failure are many and complex, that does not make it wrong to try to investigate and redress any subset of them.

Additionally, Taylor et al. (2000) assert that Foorman et al. do not adequately describe the instructional approaches in the classroom. We had explained to them that vignettes of literacy instruction of Teachers A, B, and C in the NRC Report "Preventing reading difficulties in Young Children" (Snow et al., 1998, pp. 200-204) provided further information on IC, EC, and DC instruction. Rather than acknowledge this source in their article, Taylor et al. (2000) criticize the NRC report for giving so much space to discussion of our research. Also, explicit references to the DC, EC, and IC approaches were provided in our journal article. Our dissatisfaction with the information available to us on how teachers allocated their time in this study led us to develop much more extensive classroom observation methods for our current studies. Obtaining these data pose significant challenges to the research team given the size and scope of our investigations. At any one time, we have as many as 120 teachers participating in a given study, children in two grades, and the teachers and grades being studied can vary from year to year. Nevertheless, we expect that these observations will help to explain why instructional approaches differ in effectiveness, because different approaches lend themselves a) to greater proportions of time being spent in highly effective activities, b) to promote active student involvement, and c) to promote effective teacher-student interactions. While the most effective teachers (e.g., exemplary teachers) may find ways to engage in these activities regardless of the instructional approach they follow, there is little doubt that the majority of teachers’ in-class behavior is affected by the instructional approach they follow.

In attributing motives such as “The Foorman et al. text shows little attention to or respect for the knowledge of language and literacy the children in this study may have brought from home …” (p. 8), Taylor et al. (2000), like Coles (2000), ignore the fact that there was little variability in the sample on these dimensions. In fact, we collected extensive information in these areas, which was not emphasized because of the limited variability. In evaluating these relationships, the seminal empirical synthesis of this area by Whitehurst and Lonigan (1998) should be emphasized. This synthesis showed that early literacy experiences facilitate literacy development in the early grades largely because of their impact on word level skills. Using data collected from another of our projects, Carlson, Francis, Foorman, Manke, and Fletcher (under review) replicated these findings, showing that didactic attempts by parents to teach early literacy skills influenced later reading ability because of their impact on alphabetic knowledge and phonological awareness. It is unfair for Taylor et al. (2000) to denigrate a group of researchers with words like “respect” when their textual analysis is factually incorrect and when they were told this before publication of their article. Indeed, when Taylor et al. (2000) criticize other citations in Foorman et al. (1998) because the samples are predominantly white, we wonder where is the evidence that the causes and correlates of reading achievement vary by socioeconomic status or ethnicity? We see little evidence in the research literature showing that fundamentally different explanations of how children learn or don’t learn to read are needed for children at different SES levels or ethnicities. In our at-risk sample, variability in domains related to poverty and ethnicity did not explain variability in reading achievement outcomes, in contrast to the effects of instruction.

Investigators’ Lenses can Constrain Interpretations

Taylor et al. (2000) claim that there were significant initial differences in phonemic awareness between the Direct Code (DC) and Embedded Code (EC) groups at the beginning of the year, thereby calling into question the differences in reading growth and outcomes between these groups. Pressley and Allington (2000) also suggested that the differential outcomes were attributable to differences among groups at baseline, i.e., the groups were not “matched” on phonological awareness and word reading skills in October. Again, we provided Taylor et al. (2000) with information not presented in Foorman et al. (1998) that was nevertheless ignored in their article.

First, as we pointed out above in our hypothesized gradients of generalizability, it is illogical for Taylor et al. (2000) and Pressley and Allington (2000) to attribute the DC-EC difference in word reading to differences in initial phonemic awareness, DC-IC differences to curriculum effects, and to offer no explanation for the lack of difference in word reading between IC and EC. We provided Taylor et al. (2000) with additional analyses that compared EC students with DC students with comparable initial PA. We did this reanalysis by selecting only those DC students whose initial PA score was at or below the 90th %ile of the EC group at the first wave. All EC children were included in the analysis, including children whose initial score was above the 90th %ile, but only those DC children who scored below the 90th %ile of the EC group were included. When the data were reanalyzed using this subset of the DC group, there was no difference in the distribution of PA at the first wave, indicating that the groups were quite comparable in PA at the outset. In contrast, these DC students finished the year with a mean PA score that was .3 standard deviation units higher than the whole EC group.

We also demonstrated to Taylor et al. (2000) that at each wave after the first, these DC students outperformed the EC students, and that this higher performance was evident at every level of initial PA. That is, comparing DC and EC children with comparable scores on PA in the fall, the DC children outperformed the EC children at each subsequent wave and this pattern is observed at all levels of PA in the fall. In short, the slight PA difference in the fall when the whole sample is considered does not account for the effect of instructional approach on PA. More likely, the slight difference in PA in the fall in the whole sample is due to instructional effects of DC on PA that have already taken place prior to the first occasion of measurement in mid-October. The school year in Texas begins in mid-August, and it is the first 30 lessons in the DC program that are devoted to phonemic awareness and the alphabetic principle. The majority of these lessons were completed by mid-October. Thus, the most logical conclusion is that initial PA differences were due to instructional effects—that DC includes explicit instruction in PA—and that the DC instruction is more effective in producing gains in PA.

Moreover, there is the fact that the effect of DC on learning to read words in isolation is less dependent on initial starting level as compared to the more implicit methods of instruction, whose effects on reading words depend on the child's initial level of PA. Why would instructional approach interact with initial PA in the way that it does if there is no effect of instruction? In sum, Taylor et al. picked two means out of a table in our article, performed a t-test, and came up with a different interpretation of our findings. When confronted with the illogic of their approach and additional analyses supporting our conclusions, they choose to ignore us and stick to their story.

Taylor et al. (2000) insinuate that there were fewer Grade 2 children in the DC classrooms because there were fewer students eligible for Title I services. As we explained to them and others, this decision occurred at a district level and had to do with funding decisions in terms of which schools received tutoring funds. It had nothing to do with eligibility. Dropping non-tutored children reduced the number of children in the Grade 2 DC correlation, but this did not alter the pattern of results.

Taylor et al (2000) criticize us for including age in the analysis rather than grade. They would have preferred that we analyze the data by grade and time, and included a grade by instructional group interaction. Instead, we treat age as a time-varying covariate. This approach is somewhat different from standard analysis of covariance in that age is explicitly included in the model at each occasion of measurement, not just age at the first occasion of measurement. When we include age in this way in the model, there is no effect of grade, nor is there any evidence of a grade by instructional group interaction. We included age in the analysis rather than grade because students in both grades were evaluated on the same measures and received the same instruction (i.e., the Grade 2 students received the Grade 1 curriculum at the start of the year because they were so far behind). There was no effect of grade nor grade by instructional group interaction when included in the model.

Taylor et al. are correct in their assessment that the treatment effects are larger in first grade. Be that as it may, their conclusion that the treatment effect on word reading in Grade 1 is due to the difference in PA in the fall is incorrect, and as we reported above, was shown to them to be incorrect prior to their publication of this work. More importantly, the conclusion of Taylor et al. (2000) that the smaller number of Grade 2 children in the DC classrooms biases the result in favor of the DC classrooms can be shown to be absurd. Assume for a minute that Taylor et al. (2000) are exactly correct and that differences among the groups existed in Grade 1, but not in Grade 2. Now, one must also acknowledge that, if there is no treatment effect in Grade 1 but only school effects, then regardless of whether there are treatment effects in Grade 2, all groups score higher at the end of Grade 2 than at the end of Grade 1. Thus, when the treatment effect is estimated, as was done in our analysis as the difference at the end of the year (averaged over first and second grade students), the reduced number of students in the DC classrooms in Grade 2 would systematically bias downward the DC mean. This is because the lower proportion of Grade 2 children in the DC group means that there are fewer high-scoring children contributing to the DC mean as compared to the IC-S, IC-R, and EC groups. Thus, the “problem” with our analysis alluded to by Taylor et al actually works to reduce the estimated difference between DC and the other groups.

We wonder why is it that Taylor et al. (2000) believe that the difference in PA in the fall in Grade 1 is due to a school effect when there is no evidence of a school effect in Grade 2? If there were a school effect in Grade 2, wouldn’t there be a difference in the Grade 2 instructional groups? Also, if program differences in Grade 1 are due to school effects rather than instructional effects, as Taylor et al. (2000) argue, then why did students in the DC classrooms score higher at the end of the first grade than at the start of the second grade in the DC classrooms? Keep in mind that the second grade children in the DC classrooms received IC-S instruction in the first grade because they were in first grade prior to the start of our study. And why is that pattern less apparent for the EC approach, and least apparent for the IC-R approach? Our explanation is that both DC and EC are an improvement over IC for these at-risk students, with the effect of EC being less than the effect of DC because it is not as explicit, and the effects of both instructional approaches are stronger in Grade 1 than in Grade 2. The finding of a reduced effect in Grade 2 is not surprising. The longer one waits to provide children with effective instruction, the more resistant reading problems are to change (Francis, S. Shaywitz, Stuebing, B. Shaywitz, & Fletcher, 1996; Snow et al., 1998).

Policy Implications

We agree that one study should not be the basis for forming policy. In California and Texas, the policies that Taylor et al. (2000) decry were implemented long before access to the data in Foorman et al. (1998) was possible. The forces behind these changes are open to dispute, but one factor is clearly the lack of adequate instruction in word-level reading skills in many schools. This reflected the influence of the whole-language movement and its peculiar views of the relationship of language and reading, particularly the notion that explicit teaching of the alphabetic principle was not a necessary component of beginning reading (Pressley, 1998). This conclusion may be warranted for some children, but it would be inaccurate to make this assumption for all children. Consistent with the results of Foorman et al. (1998), there is considerable evidence that explicit teaching of the alphabetic principle is a necessary (but not sufficient) component of reading instruction for children. If Foorman et al. (1998) never existed, the pendulum in the reading wars would still be swinging towards the phonics side. We agree that there is great risk that it will swing too far to the phonics side and consistently advocate balanced approaches to reading instruction. Whether one program includes more phonics, or more explicit phonics support, is independent of whether it provides quality support in reading, writing, and literacy development.

What Taylor et al. (2000) and many other reading professionals do not recognize is that the systematic misrepresentation of research such as Foorman et al. (1998) and misstatements of fact like Taylor (1998) and Coles (1998; 2000) fuel the direction of policy in the opposite direction from what they desire. By allowing our study to be characterized as a comparison of phonics and whole language, the field is telling policy-makers to accept media interpretations. Taylor et al. (2000) state that Texas has legislative mandates to teach phonics. This is factually incorrect, so that should a policy-maker in Texas read this statement, they become convinced that Taylor et al. is nothing more than polemics and that Texas should have phonics mandates. Similarly, when one reads that …” when the authors of this widely publicized study use their results as the basis for promoting specific commercial programs … they contribute to the impression that student’s reading problems will be solved if a school simply buys the right program” (Taylor et al., 2000, p. 15), it is easy to believe that the article in question (Foorman, Fletcher, & Francis, 1998) is an advertisement for these programs. In fact, this article is a critique of commercial reading programs and the focus of policy-makers on these types of programs. In this article we state, for example, that “The research on how children learn to read has been largely ignored or misapplied by developers of commercial curriculum programs” (p. 35). The commercial reading programs that were cited are examples of programs that have some form of empirical evaluation. The notion that school publishers should do more to assure the soundness and efficacy of the instructional materials they sell to schools should be compelling to anyone committed to public education.

In discussing the critique with Taylor et al. (2000), we indicated that this form of discussion was a waste of time – hence our proposed subtitle, “Why Aren’t Researchers Using Their Time to Replicate Research or to Generate New Research to Address Pressing Questions about How Children Learn to Read?”. Neither the critique nor our response is a significant contribution to reading research or practice. They serve to detract from what we see as an urgent need to use research as a basis for decision-making in education. Presently research is not used in a consistent fashion, and when research is used, it becomes a lever to enforce decisions – not to inform decisions. Part of the problem – clearly apparent in Taylor et al. and our response – is that the research base is not fully developed. We don’t have complete answers to important questions such as the conditions under which different children best learn to read.

Here the potential contributions of the critique and our response are apparent: There are issues that require additional research. A most pressing issue is the need for construct validity research on the measurement of reading comprehension skills. In addition, more research on the influence of early literacy experiences at home and in preschool settings on later reading ability is needed, particularly in relationship to SES and ethnicity. Research on teacher-student processes in large, diverse samples with teachers at different levels of expertise and with a specific focus on instructional practices that facilitate reading success at the individual student level is needed. Presently there is research in each of these domains, but it tends to focus on small groups of usually exemplary teachers and is rarely related to student outcomes (e.g., Pressley, Wharton-McDonald, Mistretta-Hampston, & Echevarria, 1998). What are the best methods for providing education and staff development to teachers? There is a lot of rhetoric and a paucity of research on these critical issues. What is the role of text decodability in promoting the early development of reading skills? Again, lots of rhetoric, lots of policy, and little data.

These examples of research questions reflect directions that we are aggressively pursuing in our research. We think the questions are important, and the findings that will be generated should influence policy – not as magic bullets, but as a long-term process in which the effects of policy changes are constantly monitored through various forms of accountability. We don’t expect others to agree with the directions we choose to pursue and don’t object to informed critiques of our research. We do object to what are essentially misrepresentations of our research at multiple levels, including Taylor et al. (2000). It is disappointing to take the time to patiently answer a number of questions and then see little of what we provided actually appear in Taylor et al. (2000) and the other venues to which we have responded. Given this inability to penetrate preconceptions and misconceptions, we patiently suggest that our time, the time of our colleagues, and the resources of national, federally-funded organizations such as CIERA would be better spent focusing on generating research and not on imagining the perceived motives of other researchers. Research and the empirical evaluation of issues in education are what we all need to be about – not about denigrating children, teachers, schools, and other researchers.

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