Chapter 33 - A Research Agenda for the Next Twenty Years

If you have read this book from its opening pages to this point, you have traveled a long road: from a crystallization crisis in a 1998 pharmaceutical plant, through four decades of contested rat-learning and staring-detection data, through mainstream biology's own increasingly sophisticated answers to the puzzle that started it all, through the deepest unresolved problems in physics and philosophy of mind, through a full toolkit of modern computational methods, and through an unflinching accounting of how those same tools could either lift human flourishing or deepen human harm. This chapter's task is to do something the book has deliberately avoided doing prematurely at any earlier stage: to prioritize. Not every research direction sketched across the preceding thirty-two chapters deserves equal investment, equal urgency, or equal claim on a young scientist's limited career runway, and a book that ends without saying so plainly would be shirking its most practical obligation to you.

The Prioritization Criteria

Before ranking anything, it's worth being explicit about the criteria I'm using, because different reasonable criteria would produce a different ranking, and you should feel free to substitute your own weighting if your values or circumstances differ from the ones assumed here. I am weighting research directions by four factors. Decisiveness: how much would a definitive result, in either direction, actually change the state of scientific knowledge, as opposed to producing another inconclusive data point in an already crowded and ambiguous literature? Feasibility: how achievable is the research with currently available technology, funding realistically obtainable by an early-career researcher, and institutional support? Safety: how favorable is the research's risk profile, per the dual-use framework of Part V, relative to its expected scientific value? And field-building value: how much does pursuing this direction help establish the rigorous methodological norms the field as a whole badly needs, independent of its specific findings?

Summary Table

Tier One: Do This First

The Global Crystallization Consortium ranks at the very top of this list, and it's worth explaining why with some care, because it is not the most technologically glamorous proposal in this book. It scores highest on decisiveness because, of every domain surveyed in Part II, industrial crystallization offers the cleanest possible separation between the mundane explanation and the resonance-favoring alternative, with a well-specified, buildable protocol capable of genuinely closing the question for this domain, one way or the other. It scores well on feasibility because every individual technical component is mature, commercially available pharmaceutical infrastructure requiring no new invention, only institutional coordination and funding. It scores excellently on safety, being about as close to zero-dual-use-risk as any proposal in this entire book. And a successful execution, regardless of outcome, would establish a genuinely valuable template for adversarial, multi-institutional, pre-registered collaboration that the rest of the field badly needs. If you are a graduate student looking for a single, concrete, career-launching project with the best combination of tractability and genuine scientific payoff, and you have any access to or connection with pharmaceutical or crystallography research infrastructure, this is where I would point you first.

The Automated Global Perception Study ranks a close second: it directly resolves the single most persistent, most frequently cited, and most methodologically confounded piece of evidence in the entire historical literature - the staring-detection controversy. It is achievable at genuinely enormous statistical power using currently existing citizen-science and mobile-app infrastructure at comparatively modest cost, and it has the specific virtue of being fundable and executable by a psychology or cognitive science researcher without requiring the more specialized pharmaceutical-industry access the crystallization protocol needs - the most broadly accessible tier-one priority for a wider range of potential researchers.

Bioelectric-pattern-memory research in the tradition of Michael Levin's work belongs in tier one too, and its presence here reflects a genuine change in how I've come to rank this whole landscape while writing this book. It is not, strictly speaking, morphic resonance research at all - it requires no non-local mechanism, and its practitioners would rightly resist having their work filed under Sheldrake's name. But it directly answers the book's original motivating question with more rigor and more existing institutional support than anything else on this list, and a young researcher joining an existing bioelectric-signaling lab, or proposing a specific extension of it - mapping bioelectric pattern information onto the "morphic unit" boundary problem using the same rigor Levin's group brings to voltage mapping - would be doing genuinely field-relevant work from inside a fully mainstream, well-funded research program, with none of the reputational risk the next chapter discusses. If you take away one specific instruction from this reordered list, let it be this: before you design a single experiment aimed at detecting non-local resonance, make sure you have first ruled out that a Levin-style local, bioelectric, or multi-level-causal mechanism doesn't already explain what you're looking at.

A practical note on getting started with any of the three tier-one directions. None of them - the crystallization consortium, the perception study, or the bioelectric baseline study - requires you to arrive with the full infrastructure already in place; all three are designed around existing infrastructure you'd be partnering into, not building from scratch. The realistic first ninety days for a graduate student pursuing the perception study, for instance, looks less like writing code and more like identifying two or three existing citizen-science platforms with an appropriate consented subject pool, drafting a one-page research proposal aimed at their existing research-partnerships team, and simultaneously recruiting a co-investigator with a public track record of skepticism toward exactly this kind of claim. The crystallization consortium's first ninety days look similar but aimed at a different kind of partner: a departmental crystallography core facility, or a pharmaceutical process-chemistry group with existing clean-room capacity sitting underused outside of active drug development cycles, approached with the specific, honest pitch that this is low-cost, low-risk, reputationally interesting science for them to support even if they have zero interest in morphic resonance themselves. The bioelectric baseline study has the shortest runway of the three: its first ninety days mean finding a developmental biology lab already running planarian or amphibian regeneration work and proposing Chapter 26's Protocol Four as a pilot on the imaging setup it already has - at $40,000 to $120,000, with no consortium and no novel instrumentation, plausibly under way within a single semester.

Tier Two: High Value, Higher Barriers

Sensor-network-based novel behavior detection in existing wildlife tracking consortia, building on Movebank and similar existing infrastructure, ranks highly on decisiveness and field-building value, but faces real feasibility barriers around the specific interdisciplinary combination of skills required and around securing the kind of cross-institutional data-sharing partnership needed - an excellent target for a research team or a well-supported PhD student with an unusually strong existing network across animal behavior and machine learning, rather than an ideal first solo project.

Diachronic embedding analysis of documented multiple-discovery cases in the history of science, tested against the rigorously formalized "adjacent possible" ripeness-score model proposed earlier, ranks highly on feasibility, requiring only publicly available historical text corpora and standard machine learning methods, achievable by a single well-trained graduate student with no need for expensive specialized infrastructure. It ranks more moderately on decisiveness, because even a positive, rigorously validated finding would establish anomalous documentary correlation rather than a confirmed mechanism, leaving real interpretive work still to be done. An excellent, genuinely achievable solo-researcher or small-team project, particularly well suited to a computational social science, digital humanities, or computational linguistics background.

Tier Three: Important, But Requires the Field to Mature First

Cross-modal genomic-behavioral co-analysis for residual anomaly detection ranks as genuinely valuable but premature for most individual researchers right now, not because the underlying question lacks merit, but because it requires specialized infrastructure access - large biobank genomic datasets with appropriate ethical clearance - that remains scarce and difficult for an early-career researcher to secure independently, and because it depends on methodological groundwork, formal statistical correction methods for high-dimensional cross-modal analysis, that the broader machine learning field itself has not yet fully resolved. This is an excellent direction for a researcher already embedded in a well-resourced genomics lab with existing infrastructure access, and an excellent longer-term thesis topic for a student willing to spend real time first building the methodological foundations.

Two smaller, self-contained methodological projects deserve mention here too, each valuable independent of any resolution of the morphic resonance question itself: the autopoietic formalization of Sheldrake's "morphic unit" concept proposed earlier, a philosophy-of-biology thesis requiring no funding beyond sustained attention and library access; and the general-purpose multiple-comparisons correction methodology for high-dimensional embedding-based methods flagged in Part IV, which I'd argue is the single highest field-wide-impact item in this entire list for a statistics or machine learning methodology PhD student, given how badly the broader applied ML field needs exactly this contribution, independent of morphic resonance entirely.

What Should Not Be Prioritized, and Why

It's worth being equally direct about what I would actively discourage a young researcher from prioritizing.

I would not prioritize further small-scale, individually-run replications of the classic staring-detection or telephone-telepathy paradigms using anything less than the full automation and statistical power of the protocol described earlier - the historical literature already contains dozens of underpowered studies of exactly this kind, and another one, however well-intentioned, is unlikely to move the needle on a question the field has been stuck on for three decades precisely because of this scale limitation. I would similarly not prioritize research explicitly seeking direct physical or quantum-mechanical evidence for a literal, distance-independent morphic field, given the serious physics concerns raised earlier, over research targeting the narrower, information-theoretic, mechanism-agnostic formulation developed across Part III and operationalized throughout Part IV - the former requires overturning extremely well-tested physical principles with no current positive evidence pointing that direction, while the latter is tractable, fundable, and scientifically valuable regardless of its eventual outcome.

How This Ranking Will Age

I want to be honest about something the tiered structure above can't fully convey: this ranking is a snapshot, made at a specific moment, of a landscape that will move under it. Two kinds of movement are worth naming specifically, because each would require revisiting the ranking rather than treating it as fixed.

The first is scientific. If a rigorously executed Protocol Four, of exactly the kind described in the previous chapter, finds that bioelectric or multi-level-causal mechanisms genuinely do account for a specific class of claimed anomaly, that finding should pull even more research attention toward tier-one bioelectric work and away from resonance-specific protocols targeting the same domain - the ranking should update in real time as evidence comes in, not remain frozen at the priorities that seemed reasonable before any of this research had actually been run. The second is infrastructural. Several of the feasibility judgments in this chapter - the cost of clean-room time, the availability of citizen-science subject pools, the maturity of cross-modal tooling - are contingent on the state of research infrastructure as this book was written, and infrastructure costs in exactly these areas have historically fallen faster than most researchers plan for. A protocol ranked "tier two" today, mainly because of a specific cost or access barrier, could plausibly become tier one within five years if that barrier falls, the way the Automated Global Perception Study's entire feasibility case depends on smartphone and citizen-science infrastructure that simply didn't exist when Sheldrake first proposed the underlying experiment.

The practical instruction this leaves you with: treat this chapter as a starting framework to argue with, not a settled conclusion to defer to. If you're choosing a research direction from this list two or three years from now, redo the feasibility and cost estimates with current numbers before committing - the specific dollar figures and team compositions in this chapter have a shelf life, even though the underlying prioritization logic, decisiveness weighed against feasibility weighed against safety weighed against field-building value, should remain useful considerably longer.

A Note on Portfolio Thinking

Think about this research agenda the way a thoughtful investor thinks about a portfolio, rather than the way a gambler thinks about a single bet. No single study in this list, however well-designed, will single-handedly resolve the morphic resonance question; the honest expectation, given everything Parts II and III established, is that most individual studies conducted along these lines will produce null or ambiguous results, exactly as most individual studies in any young, methodologically maturing research area do. The value of the research agenda described in this chapter lies in its cumulative, portfolio-level effect: a decade of well-designed, pre-registered, adversarially collaborative studies across these several tiers, whatever any single study's individual outcome, will leave the field in a qualitatively better epistemic position than four decades of smaller, disconnected, methodologically compromised studies have managed to achieve - and that field-level improvement is itself a genuinely worthwhile career contribution, even for a researcher whose own individual studies happen to return null results.

Looking Forward

With a prioritized agenda now on the table, Chapter 34 turns from the specific research directions to something more personal: practical, concrete advice for a young scientist actually considering building a career, or even just a single thesis, around any part of the territory this book has covered - and a final, honest reflection on what any of it will have meant.