When Research Optimises the Wrong Future: Toward an Order-Based Taxonomy of Inquiry

by Zaky Jaafar

Contemporary universities expend vast intellectual, financial, and institutional resources on research that is undoubtedly necessary, yet increasingly insufficient when judged against the scale of systemic threats confronting society. The problem is not methodological weakness, nor a lack of diligence, but a persistent mismatch between the depth of inquiry and the depth of the challenges faced. Research is overwhelmingly directed toward problems that are legible within existing systems, while questions concerning the viability, direction, and desirability of those systems themselves are marginalised. In this condition, universities risk becoming highly efficient engines of performative problem-solving, addressing symptoms with sophistication while leaving structural trajectories largely untouched.

This tendency is visible across domains. For example, in the Southeast Asian palm oil context, studies on water pollution, deforestation, or labour conditions are lower-order not because they are trivial, but because they implicitly accept palm oil’s structural centrality. This orientation is reflected empirically in the research landscape itself. Bibliometric and review studies show that the overwhelming majority of academic publications on palm oil in Southeast Asia focus on environmental impacts, certification schemes, yield optimisation, and labour governance within the existing plantation regime, while comparatively few studies treat as a primary research question the strategic viability of palm oil as a long-term national development pathway in relation to food security, land sovereignty, or ecological limits (Euler et al., 2016; Cramb & McCarthy, 2016; Pye & Bhattacharya, 2013). In this sense, lower-order research is abundant not by accident, but because prevailing research agendas are structured around managing the consequences of an accepted system rather than interrogating its necessity or alternatives.

A similar pattern can be seen in contemporary research on digital infrastructure. Faced with the escalating energy and water demands of data centres, a great deal of research focuses on improving water-efficient cooling technologies. This work is technically impressive and immediately applicable. Yet it assumes that the current paradigm of energy-intensive, centralized computing will continue indefinitely. A higher-order research question would instead ask whether alternative computing architectures, such as low-energy computing, edge computing, neuromorphic chips, or fundamentally different information-processing paradigms, might render the problem of massive data-centre cooling obsolete or marginal. The latter line of inquiry interrogates not the efficiency of the system, but the necessity and trajectory of the system itself. What is missing, therefore, is not more research, but a conceptual apparatus that allows universities to distinguish between different orders of research. Such a distinction is not intended to dismiss reductive or applied studies, but to restore an institutional capacity to perceive systemic threats and long-term trajectories. Without this distinction, research agendas remain vulnerable to market logic, funding fashions, and bibliometric incentives, producing outputs that are productive yet strategically shallow.

To address this, the notion of an Order of Research taxonomy can be introduced as a diagnostic rather than prescriptive framework. Although classification itself risks fragmentation, it becomes necessary precisely because research cultures are already fragmented in ways that obscure systemic depth. The purpose of such a taxonomy is to clarify the level at which a study intervenes in a system, measured not by duration or technical difficulty, but by the depth of the assumptions it questions.

This framework draws implicitly on several established theoretical traditions. Systems theorist Donella Meadows distinguishes between shallow leverage points, such as parameters and efficiencies, and deep leverage points, such as system goals and paradigms, arguing that most interventions cluster at the former despite their limited transformative potential (Meadows, 1999). Political economy, particularly in the work of Karl Polanyi and Ha-Joon Chang, similarly exposes how economic systems naturalise themselves, rendering structural alternatives unthinkable while encouraging technical refinement within dominant regimes (Polanyi, 1944; Chang, 2002). In sustainability and transition studies, Geels’ multi-level perspective highlights how research overwhelmingly stabilises existing socio-technical regimes rather than enabling transitions beyond them (Geels, 2002). The proposed taxonomy makes these implicit distinctions explicit within the governance of research itself.

If the notion of research order is to function as more than a rhetorical critique, it must be made operational without becoming technocratic. One way to do this is to articulate a schematic of research orders that is descriptive rather than prescriptive, and diagnostic rather than evaluative. Such a schematic does not rank intelligence or rigor, but identifies the depth of systemic assumption at which a study operates.

At the most immediate level lies what may be called Order I research. This form of inquiry focuses on localized variables within a stable system. It asks how to improve efficiency, reduce harm, or enhance performance without questioning the underlying structure. Studies on water-efficient cooling technologies for data centres, emission reduction techniques within palm oil plantations, or improved logistics in global supply chains fall into this category. Order I research is indispensable. It produces actionable results, feeds engineering and policy workflows, and often delivers rapid returns. Yet it remains bounded by what Meadows would describe as parameter-level interventions, operating entirely within accepted system goals (Meadows, 1999).

A step deeper is Order II research, which addresses interactions, feedback loops, and trade-offs within the system. Here the concern is no longer isolated variables, but systemic behavior. Research on how cooling technologies interact with regional water stress, energy grids, and climate feedbacks, or how palm oil expansion reshapes rural labor markets and ecological thresholds, belongs to this order. Order II research often adopts interdisciplinary methods and begins to expose contradictions within the system, yet it still assumes the system’s continuity. It asks how to manage complexity, not whether the complexity is itself a symptom of a deeper structural misalignment.

Order III research marks a qualitative shift. At this level, the system itself becomes the object of inquiry. The research question is no longer how to improve data centres, but whether the prevailing model of energy-intensive, centralized computing is a rational technological trajectory under climate and resource constraints. Similarly, in agriculture, the question becomes whether dependence on a monocrop export regime undermines long-term food sovereignty and ecological resilience. This is the domain of political economy, transition studies, and strategic foresight. As Geels’ multi-level perspective suggests, such research interrogates regimes rather than niches, and opens space for alternative configurations rather than incremental adaptation (Geels, 2002). It is here that Chang’s critique of development orthodoxy and Polanyi’s analysis of market society become especially salient, as both expose how systems naturalize themselves and foreclose alternatives through institutional momentum (Chang, 2002; Polanyi, 1944).

Finally, one may tentatively identify Order IV research, which addresses paradigms, values, and civilizational trajectories. This is the most difficult and least institutionally comfortable order. It asks what goals systems ought to serve in the first place. In computing, this might involve questioning growth-driven data accumulation as a social good. In agriculture, it might involve reframing land, labor, and food not as commodities but as elements of collective survival and cultural continuity. Order IV research is explicitly normative, but not ungrounded. It draws on history, ethics, philosophy of technology, and long-term scenario reasoning. While often accused of being speculative, it corresponds precisely to Meadows’ deepest leverage points: the power to transcend paradigms rather than merely optimize within them (Meadows, 1999).

Seen in this way, higher-order research does not necessarily imply longer timeframes, though it often does. A speculative study on alternative computing architectures may be conceptually higher-order than a decade-long optimization project if it challenges core assumptions about energy, scale, and growth. Order, therefore, refers not to duration or difficulty, but to depth of intervention in the logic of the system.

Once such a schematic is articulated, the structural problem with contemporary research governance becomes clearer. Most university KPIs and grant evaluation mechanisms are implicitly optimized for Order I and, to a lesser extent, Order II research. Citation counts reward dense, self-referential literatures rather than cross-paradigmatic synthesis. Impact factors privilege incremental contributions to established fields. Short grant cycles favor problems that can be scoped, measured, and delivered within existing frameworks. Industry-linked funding further reinforces system-preserving inquiry, since markets have little incentive to finance research that questions their own premises.

The consequence is not that higher-order research is banned, but that it is rendered institutionally irrational. Scholars pursuing Order III or IV questions face longer gestation periods, fewer “safe” publication outlets, and higher reputational risk. Over time, this produces a form of epistemic selection: universities become very good at solving problems that do not threaten prevailing economic and technological trajectories, and very poor at anticipating systemic failure. As Polanyi warned, societies that subordinate knowledge production entirely to market logic risk losing the capacity for self-correction until crisis forces it upon them (Polanyi, 1944).

Introducing research order as an explicit evaluative lens would not replace bibliometrics or performance indicators, but it would contextualize them. A university could, for instance, ask not only how productive a research portfolio is, but how it is distributed across research orders. An institution saturated with Order I excellence but devoid of Order III and IV inquiry may be efficient, yet strategically blind. Conversely, a modest investment in higher-order research could yield disproportionate long-term value by informing policy direction, infrastructural choice, and national resilience.

Ultimately, the purpose of this framework is not administrative tidiness, but intellectual honesty. In a century marked by climate instability, technological acceleration, and geopolitical uncertainty, the greatest risk facing universities is not irrelevance, but misplaced relevance. By naming and legitimising higher-order research, universities reclaim their role not merely as engines of innovation, but as custodians of judgment about which futures are worth optimizing for.

 A schematic articulation of research orders can be summarised as follows.

Table: Schematic Taxonomy Order of Research

Order of Research	Primary Object of Inquiry	Core Question Asked	Underlying Assumption	Typical Methods & Disciplines	Illustrative Examples	Primary Risk if Over-Dominant
Order I: Parametric / Optimisation Research	Isolated variables within an existing system	How can this be made more efficient, safer, or less harmful?	The system is given, stable, and desirable	Engineering optimisation, applied sciences, technical modelling	Water-efficient cooling for data centres; pollution mitigation in palm oil plantations	Perfects an unsustainable system without questioning its trajectory
Order II: Systemic Interaction Research	Interactions and feedbacks within a system	How do system components interact and generate unintended effects?	The system persists but requires better management	Interdisciplinary analysis, systems modelling, impact assessment	Energy–water–climate feedbacks; socio-ecological effects of plantation economies	Manages complexity while leaving core structures intact
Order III: Structural / Regime-Level Research	The system itself as a historical construct	Should this system continue, and what alternatives are viable?	Systems are contingent and replaceable	Political economy, transition studies, comparative analysis	Alternative computing architectures; shifts from export monocrops to food-sovereign agriculture	Marginalised as political or speculative despite strategic relevance
Order IV: Paradigmatic / Civilisational Research	Goals, values, and worldviews shaping systems	What purposes should systems serve in the first place?	Dominant paradigms are neither neutral nor inevitable	Philosophy of technology, ethics, history, critical theory	Questioning growth-driven data accumulation; reframing land and food beyond commodity logic	Dismissed as impractical, leading to loss of anticipatory capacity

This taxonomy clarifies that higher-order research does not necessarily entail longer timeframes, although it often does. Rather, it intervenes at deeper leverage points. A speculative inquiry into low-energy or post-growth computing may be higher-order than a decade-long optimisation project if it challenges core assumptions about scale, growth, and energy use. Order refers to epistemic depth, not temporal length.

The value of this framework lies in its institutional implications. Contemporary research evaluation regimes overwhelmingly privilege Order I and, to a lesser extent, Order II research. Citation counts, impact factors, and h-indices reward alignment with established literatures and dense academic networks. Short grant cycles favour projects with predictable outputs and low epistemic risk. Industry-linked funding reinforces system-preserving inquiry, since markets have little incentive to finance research that questions their own premises. The result is not an explicit prohibition of higher-order research, but its gradual institutional marginalisation.

Empirical studies in the science of science consistently show that the overwhelming majority of published research is incremental rather than transformative, with genuinely system-challenging or paradigm-disrupting work constituting only a small fraction of total output. Large-scale bibliometric analyses demonstrate that most scientific papers consolidate existing knowledge structures rather than disrupt them, while transformative research appears statistically rare and increasingly uncommon over time (Foster et al., 2015; Wu, Wang, & Evans, 2019). This skew is reinforced by contemporary research evaluation regimes that rely heavily on citation counts, journal impact factors, and h-indices, which systematically reward alignment with established literatures and dense citation networks rather than epistemic risk or structural novelty (Hicks et al., 2015; San Francisco Declaration on Research Assessment [DORA], 2013). Funding mechanisms further amplify this imbalance. Studies of peer review and grant allocation show a pronounced bias toward “safe” projects with predictable outcomes, disadvantaging high-risk or conceptually radical proposals that challenge dominant paradigms (Boudreau et al., 2016; OECD, 2021). Short grant cycles and milestone-driven assessments intensify this conservatism by privileging research that can demonstrate rapid, measurable deliverables over work that interrogates system-level assumptions. Finally, industry-linked and mission-oriented funding tends to reinforce existing technological and economic regimes, since market actors have limited incentive to support research that questions the foundational premises of their own business models or growth trajectories (Mazzucato, 2018; Polanyi, 1944). The cumulative effect is not the explicit exclusion of higher-order research, but its gradual institutional marginalisation, as evaluation, funding, and publication systems converge to favour optimisation within existing systems rather than inquiry into their necessity, limits, or alternatives.

Over time, this produces a form of epistemic selection. Universities become adept at refining systems whose long-term sustainability is increasingly doubtful, while losing the capacity for anticipatory judgment. Polanyi warned that societies subordinating knowledge production entirely to market logic eventually lose the ability to recognise systemic breakdown until crisis forces recognition upon them (Polanyi, 1944). In such a context, productivity becomes decoupled from wisdom.

Introducing the concept of research order does not require abandoning existing metrics or applied research priorities. Rather, it situates them within a broader evaluative ecology. Universities could ask not only how much research is produced, but how it is distributed across research orders. An institution saturated with Order I excellence but devoid of Order III and IV inquiry may appear competitive while remaining strategically blind. Even modest institutional space for higher-order research could yield disproportionate long-term value by informing policy direction, infrastructural choices, and national resilience.

Ultimately, the purpose of this framework is not administrative tidiness, but intellectual honesty. In an era defined by ecological limits, technological acceleration, and geopolitical uncertainty, the greatest risk facing universities is not irrelevance, but misplaced relevance. By explicitly recognising different orders of research, universities reclaim their role not merely as problem-solvers for existing systems, but as custodians of judgment about which futures are worth optimising for.

(Disclaimer – This article uses AI assistance for extracting the relevant references. But the structural idea and framing of discussions is original by the author)

References

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