Try, Fail, Learn, Repeat

From Problem to Practice in Music Teacher Education Research

By NAfME Member Ann Marie Stanley

This article was first published in the February 2026 issue of Journal of Music Teacher Education.

In my previous column, I emphasized the critical importance of collaboration in advancing our field of music teacher education (Stanley, 2024). More recently, I called for substantive research into admissions practices and their downstream effects on the music teacher shortage (Stanley, 2025). In both columns, I wrestled with how we identify problems in our field—and both ended with calls for research-based solutions. As I prepared for our biennial Society for Music Teacher Education (SMTE) symposium at Butler University this October, reviewing the presentation and poster abstracts, I began to wonder whether our field demonstrates a troubling imbalance. Have we become exceptionally good at diagnosing what ails music teacher education, but less adept in our capacity for documenting, testing, and refining solutions? We often gesture at possible interventions in implications sections, but rarely are they at the center of the inquiry. I include myself and my closest colleagues in this observation (e.g., Johnson et al., 2025; West et al., 2021). In these two recent publications, my co-authors and I identified serious problems with music teacher education’s urban and rural teacher professional development structures. We presented quite a few solutions, but worded these mostly in terms of suggesting issues for other, future researchers and professors to take on and study.

This is not a new observation in the broader landscape of teacher education. When the Journal of Music Teacher Education created the Analyses of Programs, Practices, and Policies (APPP) format several years ago, it was precisely to address a gap between problem identification and solution implementation (Conway, 2023). The APPP format asks scholars to move beyond “here’s what I do in my program” toward rigorous analysis that connects practices to scholarship, provides thick description that others could replicate, offers critical reflection on what worked and what didn’t, and considers transferability across contexts. In other words, APPP was designed to bridge the space between identifying a problem and documenting attempts to solve it.

In the 2025 SMTE symposium program, I am thrilled to see the range of thoughtful work. For example, to name just a few topics, SMTE researchers are vividly documenting mental health struggles among music education majors, and structural issues that make life difficult for MTEs who are mothers. They are methodically tracing the structural barriers facing potential music educators. Others note a major gap between what preservice teachers believe about creative musical activities, and what they actually implement 5 years into their careers—including the sobering finding that 40% of participants in the follow-up portion of one study aren’t teaching music anymore (Talbot & Piazza, 2025). But as I read through our SMTE conference abstracts—all creative, rigorous, and addressing critical issues in our field—I kept returning to an uncomfortable question: Are we still operating primarily in diagnostic or problematizing mode? These articles and studies are vital contributions. We need to understand the scope and nature of our challenges in music teacher education. But at what point does continued diagnosis without documented testing of solutions become a form of avoidance?

I’m not suggesting that research identifying problems is without value: quite the opposite. The work being presented at the SMTE biennial symposium represents some of the most important thinking in our field. I’m also not suggesting that everyone should stop studying problems and start implementing solutions tomorrow. What I am suggesting is that we need to examine why our field has developed such strong capacity for problem identification while our capacity for implementation research remains underdeveloped. This column uses our conference submissions as a mirror—a way to reflect on our collective scholarly practices. What do our research questions reveal about what we’re comfortable studying? What gaps in our conference program might point to gaps in our field’s capacity?

In what follows, I’ll analyze patterns in our conference submissions, pose some uncomfortable questions about our scholarly incentive structures, and argue that the APPP format—and more broadly, a shift toward implementation research—offers a path forward. This isn’t about criticizing individual scholars or particular studies. It’s about asking whether our field has the right balance between identifying what’s broken and documenting our attempts to fix it.

Looking across the abstracts for our October 2025 conference, several patterns emerge. We have multiple articles examining student mental health and the unsustainable workload of music education majors—vital work documenting credit hour overload, hidden labor, perfectionism, and the stress that accompanies teacher preparation programs. We have presentations tracing structural barriers in the profession, including the critical work examining how music educators of color experience repeated obstacles at multiple career junctures. We have studies documenting gaps between what teachers learn in preparation programs and what they actually do in schools.

All the projects share important characteristics: problems identified with clarity and rigor, findings grounded in solid methodology, and implications for practice provided—often in the form of “programs should consider” or “music teacher educators need to address” statements. What I see less of is documentation of someone’s actual attempt to (a) implement the recommendations from previous research, (b) track what happened when they did, and (c) analyze why the implementation succeeded or failed.

A thorough content analysis of the program is beyond the scope of this column (although that would make a great research study for someone reading this right now!). For this column, I read the program and asked myself: “Is the essence of this scholarship (a) describing what currently exists, (b) proposing something, or (c) testing, evaluating, or examining how something WORKS in practice?”

My back-of-the-envelope calculations reveal, though, that about 50%–60% of the presentations and posters are works where the main purpose is to describe, explore, or examine what currently exists:

• Phenomenological studies exploring lived experiences.
• Surveys examining current demographics or state of things or studies identifying gaps, barriers, or relationships between variables.
• Research questions like “What are teachers’ experiences with X?” or “How do these two things relate?”

Another 10%–15% are projects intended to propose, design, or present something new:

• “This study proposes a framework for . . .” “We present a model for . . .”
• “This article offers a six-step approach to . . .”
• Design studies creating new curricula or programs.

Both these two groups together (about 70%) I lumped into the “explore problems or propose solutions” category. About 25% are studies where the main purpose is to test, evaluate, or examine how existing frameworks, instruments, or practices actually work in real settings:

• Follow-up or longitudinal studies tracking what happened to earlier cohorts or interventions over time.
• Validation studies testing how an instrument, assessment, or some kind of change or intervention works in a music education context.
• Implementation studies examining how teachers actually use or apply a particular pedagogy, curriculum, or approach in their classrooms.
• Self-study or action research documenting and analyzing how practices unfold in the researcher’s own teaching context.
• Research questions like “Can we now reliably measure X?” or “How did teachers implement Y?” or “What happened five years later?”

Consider the trajectory of one research finding in our field. A study documents that music education majors face crushing workloads. The implications section suggests that programs should reconsider credit hour requirements. The study is published, presented at conferences, and cited by other scholars. This is a hot topic right now, and because of the scholarship in this field, I know that multiple music teacher preparation programs have recently—and drastically—reduced music education degree credit hours. It is time to examine those follow-ups. I’m curious if programs might feel pressure to “prove” the cuts didn’t hurt quality, leading to assessment theater that consumes the time saved. Or conversely, honest assessment might reveal actual gaps, creating political problems for administrators who championed the changes.

I have so many questions. What organizational resistance did these programs encounter? Did it help student well-being? Did it create new problems? Are there are any unintended consequences from these changes, such as lower credit hour counts in a unit suddenly resulting in a smaller funding allocation? What is the experience of a teacher who went through a newly truncated degree program? Did they inadvertently miss important information?

When forced to cut, do departments entrench around different pedagogical philosophies? Which gets protected—methods courses? conducting? music theory? The process of deciding what’s “essential” could either foster healthy curriculum review or create lasting faculty divisions. Did courses that remain become more densely packed, recreating the workload problem in disguise? Or did programs shift requirements to “highly recommended” or unpaid assistantships/observations?

Students with means might fill gaps through summer programs, private lessons, or graduate work—while others can’t. This could inadvertently advantage already-privileged candidates. If students have more breathing room, do cohorts become stronger (more time to collaborate) or weaker (less shared struggle/identity)? Does retention improve but cohesion suffer?

Fewer credits might mean faculty teach less, but the density of curriculum design, student support, and field supervision could increase. Small programs might lose faculty lines, leaving those remaining with worse ratios. On the contrary, students might pursue double majors, minors, or service learning that makes them more interesting, versatile teachers. Mental health improvements might reduce attrition, strengthening the teacher pipeline, and graduates might enter the profession less burned out, improving retention in K–12 schools. Did the material students chose to learn (when not overbooked with required coursework) result in more creative inservice teacher practices?

To be clear: Our conference program contains many presentations examining specific interventions, documenting program changes, exploring alternative approaches to teacher preparation. But a close read of the abstracts show me when we do document interventions, we often stay within the boundaries of what we control, for example, examining what happens during, say, a university course load redesign, rather than following teachers into the rest of their university experience and then on into the profession to have a true sense of what happened after the changes went into effect.

So why do we remain in diagnostic mode? If we know that implementation research is needed, if we’ve created formats like APPP specifically to encourage it, why does our work still tilt so heavily toward problem identification? The answer does not reflect a failure of individual scholars. Rather, I believe we’re caught in a web of structural incentives, methodological challenges, and reasonable fears that make implementation research genuinely difficult, but difficult doesn’t mean we should avoid it.

Let’s be honest about how academic careers work. Traditional empirical research—the kind that identifies gaps, documents problems, and establishes that something is statistically significant—fits neatly into existing reward structures. Such studies can be completed within a reasonable timeframe for a dissertation or a tenure clock. They produce clean findings that reviewers can evaluate using established criteria. They demonstrate mastery of research methods in ways that hiring committees and promotion committees understand.

Implementation research is messier. Testing a new admissions approach might take 5 years before you can assess retention outcomes. Documenting what happens when you redesign a program based on research recommendations means risking public failure. It requires collaboration across institutional boundaries, which means coordinating schedules, navigating institutional review board (IRB) approvals at multiple sites, and managing the inevitable disagreements about what “fidelity to the intervention” even means. At the end of all that work, you might discover that your carefully designed solution . . . didn’t work. Or worked only in some contexts. Or worked for reasons you didn’t anticipate and can’t quite explain.

How do we reward faculty who attempt this work? Do our tenure and promotion guidelines recognize APPP submissions as equivalent to traditional empirical research? When we write letters evaluating colleagues for promotion, do we value their documentation of a failed experiment as much as we value their successful identification of a new problem? I’m not certain we do. Longitudinal and replication research may take longer and present different challenges for researchers conscious they need to produce a certain quantity of scholarship over a finite time period in between academic review. Our comfort level with research may also depend on what we think will get published.

This leads to a related question: What happens when implementation research fails? In a study of professional development (West et al., 2021), we designed what we thought was exemplary PD—sustained, music-specific, collaborative, inquiry-based, teacher-directed—and watched as six of eight teachers abandoned it within 5 months. That hurt to document. But those failures taught us more about the organizational constraints on teacher learning than any of our “successful” PD studies had revealed.

Think about the “kazoo bubble” scenario I posed in my column on university admissions in this journal (Stanley, 2025):

What if one year at Penn State, there are 12 kazoo players who we think could make phenomenal future music educators, yet the kazoo studio is full with 18 kazoo majors already? Do we admit anyway in service of our hope that this decision will pay off by augmenting the number of music teachers put into the world? Do we decide that the pain of having too many kazoos in the class of 2029 will eventually be worth it? We have to acknowledge this “kazoo bubble” will have drastic financial and organizational impact, and possibly diminish the experience for the students who have to learn in an overcrowded, overcommitted studio with intense competition for opportunity. And bigger question: is it Penn State’s job to redirect our limited resources now to help one profession, later?

What if a school of music decides to admit more students who show potential as music educators even though it creates temporary enrollment imbalances? Somebody needs to try this and document what happens—including the organizational pain points, the faculty resistance, the resource reallocation challenges, and yes, whether it eventually helps address the teacher shortage. But who wants to be the person who documents that their institution’s bold new approach created chaos and had to be abandoned?

The field needs documentation of failed experiments. We need to know what doesn’t work and why. I suspect this is partly because journals favor positive results (though I’d argue JMTE’s APPP format creates space for this kind of honest reporting). But it’s also because it takes a particular kind of professional courage to say publicly, “We tried this thing that seemed like a good idea based on the research, and it was a disaster.” Until we make it professionally safe—even professionally valuable—to find places and the means to try big changes, and document our efforts, we may not know for sure if the implications for practice we suggest are truly valid.

Here’s an uncomfortable truth: Implementing change is hard in ways that studying problems is not. Studying the mental health crisis among music education majors requires designing a good survey, recruiting participants, analyzing data, and writing up findings. Important work, certainly. But implementing a solution means convincing your faculty colleagues to reduce credit hour requirements, navigating institutional approval processes, managing pushback from accreditation bodies, reallocating limited resources, and potentially harming some students (those whose studio or ensemble experience suffers from the enrollment changes) to help others.

Consider Talbot and Piazza’s (2025) finding that 40% of participants were no longer teaching music 5 years after graduation. This wasn’t a primary research question—it was an incidental finding that appeared during follow-up. How many other critical implementation failures are we missing because following teachers into the field is methodologically challenging? Tracking cohorts longitudinally requires sustained funding, institutional cooperation, and researchers willing to commit to a project that might not produce publishable results for years. It’s far simpler to survey this year’s graduating class about their preparedness than to follow them into schools and document what happens.

We are not lazy. We are operating in a system that makes implementation research genuinely difficult to accomplish while making problem identification relatively straightforward. When faced with the choice between difficult and straightforward, while operating under the pressures of promotion timelines and grant cycles, we often choose the path of least resistance. Perhaps, the most frustrating aspect of implementation research in music teacher education is that many of the problems we’ve identified require systemic solutions that no individual researcher can implement or study. You can’t fix the teacher shortage from a single institution. You can’t change accreditation requirements as one faculty member. You can’t address the lack of diversity in applicant pools by modifying your local audition practices if the pipeline issues start in elementary school.

This creates a genuine dilemma. If we wait for systemic change before studying implementation, nothing will move. But if individual institutions make changes in isolation, we can’t generalize from their experiences. What we may need is coordinated implementation research across multiple institutions—exactly the kind of work that’s hardest to fund, hardest to coordinate, and hardest to publish because it doesn’t fit neatly into existing journal categories. In addition, I’m acutely aware of the irony here. I’m writing a column that identifies a problem (our field’s emphasis on problem identification) without documenting my own attempts to solve it. I’m operating in exactly the mode I’m critiquing, but perhaps the discomfort is instructive.

The Journal of Music Teacher Education APPP format exists precisely to address these challenges. It provides a legitimate scholarly outlet for implementation documentation that doesn’t fit traditional empirical research categories. It values thick description of context, which means you can document the messy realities of trying to change programs. It requires critical analysis, which means you can—and should—discuss what didn’t work. It asks for explicit attention to transferability, which pushes authors to help readers understand which aspects of their implementation might apply elsewhere and which are context-specific.

Imagine if future conference submissions included documentation of a program that reduced credit hours and tracked effects on student well-being and program enrollment more than three years; analysis of an admissions pilot that tried alternative audition requirements and honestly assessed the organizational consequences; a multi-institutional collaboration testing whether specific program modifications help retain early-career teachers. These would be careful documentation of implementation attempts—what the research literature suggested, what we tried, what organizational factors shaped implementation, and what we’d do differently next time.

This is what the research-to-practice pipeline should look like: Empirical research identifies problems; APPP documents implementation attempts; more empirical research evaluates effectiveness at scale. Right now, we have plenty of the first step, very little of the middle step, and can’t get to the third step without it.

A Call to Action

For individual faculty and graduate students: Before your next conference submission, ask whether you’re studying a problem or testing a solution. Review the “implications for practice” sections in articles you’ve published. Have you tried implementing them? Could you document what happened?

For institutions: Create cross-institutional “implementation cohorts” where multiple programs try the same intervention and compare notes. Build longitudinal tracking into program infrastructure. Recognize APPP scholarship in tenure and promotion decisions.

For SMTE: Consider a dedicated conference strand for implementation studies. Invite “three years later” follow-ups to previous presentations. Create recognition for best implementation documentation.

For JMTE: Continue promoting APPP submissions. Consider asking authors of empirical studies to include implementation notes—what would someone need to know to try this in their context?

Our SMTE conference sessions reveal the questions keeping MTEs up at night. We should be concerned about student well-being, about equity and access, about the gaps between preparation and practice. But our field’s maturity will ultimately be measured not by our diagnostic sophistication but by our willingness to attempt research-based changes.

This won’t be easy. It requires vulnerability to document failures. It requires patience because implementation takes time. It requires collaboration because no one can do this alone. The next great contribution to music teacher education might not be discovering a new problem. It might be documenting how we attempted to solve an old one—including all the messy, complicated, context-specific realities that made implementation harder and far less predictable than we expected. That’s the work ahead.

References

Conway C. M. (2023). Analyses of programs, practices, and/or policies submissions to the JMTE: What do authors need to consider? Journal of Music Teacher Education, 33(1), 3–10.

Johnson D. J., Stanley A. M., Nowak T. E. (2025). Voices of rural music teachers: Negotiating professional and proximal community in rural music education. Bulletin of the Council for Research in Music Education, 245, 30–47.

Stanley A. M. (2024). Elevating our work, intensifying our progress. Journal of Music Teacher Education, 34(1), 13–16.

Stanley A. M. (2025). Missing voices: A research agenda for music education admissions practices. Journal of Music Teacher Education, 34(2), 10–14.

Talbot B. C., Piazza E. (2025, October 23). Changing perceptions from college to classroom: Creative musical activities among early career music teachers [Paper presentation]. 2025 Symposium on Music Teacher Education, Indianapolis, IN, United States.

West J. J., Stanley A. M., Bowers J. P., Isbell D. S. (2021). Attrition, (de)motivation, and effective music teacher professional development: An instrumental case study. Bulletin of the Council for Research in Music Education, 229, 7–28.

About the author:

Ann Marie Stanley, Ph.D., Chair of the NAfME Society for Music Teacher Education, is Director of the School of Music and Professor of Music Education at The Pennsylvania State University. Before her appointment at Penn State, Stanley was Professor of Music and Associate Dean for Graduate Studies at Louisiana State University’s College of Music and Dramatic Arts, and Associate Professor of Music Education at the Eastman School of Music (2007–2016). Stanley taught public school general music for seven years in California. In addition to a doctorate from the University of Michigan, she has degrees in oboe performance from Wichita State University. Stanley is the chair of the Society for Music Teacher Education, and she co-authored the Oxford Handbook of Preservice Music Teacher Education in the U.S. (2020). She has published more than 30 textbook chapters and research studies in major music journals, including Arts Education Policy Review, Bulletin for the Council for Research in Music Education, Journal of Music Teacher Education, and Research Studies in Music Education.

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