The ocean flows because it is forced by winds, tides and exchanges of heat and freshwater with the overlying atmosphere and cryosphere. To achieve a state where the defining properties of the ocean (such as its energy and momentum) do not continuously increase, some form of dissipation or damping is required to balance the forcing. The ocean circulation is thought to be forced primarily at the large scales characteristic of ocean basins, yet to be damped at much smaller scales down to those of centimetre-sized turbulence. For decades, physical oceanographers have sought to comprehend the fundamentals of this fractal puzzle: how the ocean circulation is driven, how it is damped and how ocean dynamics connects the very different scales of forcing and dissipation. While in the last two decades significant advances have taken place on all these three fronts, the thrust of progress has been in understanding the driving mechanisms of ocean circulation and the ocean's ensuing dynamical response, with issues surrounding dissipation receiving comparatively little attention. This choice of research priorities stems not only from logistical and technological difficulties in observing and modelling the physical processes responsible for damping the circulation, but also from the untested assumption that the evolution of the ocean's state over time scales of concern to humankind is largely independent of dissipative processes. In this article, I illustrate some of the key advances in our understanding of ocean circulation that have been achieved in the last 20 years and, based on a range of evidence, contend that the field will soon reach a stage in which uncertainties surrounding the arrest of ocean circulation will pose the main challenge to further progress. It is argued that the role of the circulation in the coupled climate system will stand as a further focal point of major advances in understanding within the next two decades, supported by the drive of physical oceanography towards a more operational enterprise by contextual factors. The basic elements that a strategy for the future must have to foster progress in these two areas are discussed, with an overarching emphasis on the promotion of curiosity-driven fundamental research against opposing external pressures and on the importance of upholding fundamental research as the apex of education in the field.
In this article, I offer a personal perspective on the evolution of physical oceanography and on the measures that, in my judgement, ought to be taken to nurture a future abounding with the creativity and originality that have historically characterized the field. This article has been solicited by the Challenger Society for Marine Science and the UK Scientific Committee on Oceanic Research as part of their ‘Prospectus for UK marine science for the next 20 years’ joint project, and seeks to contribute to laying the ground for the writing of a scientist-driven national strategy for marine science.
The rationale of the perspective presented here is that, lacking clairvoyance, guidance for the future may be sought in the past and in the evolution of a more mature sister field (atmospheric science) in recent decades. By weaving these two threads of evidence, I will argue that most, if not all, of the scientific breakthroughs in physical oceanography of the next 20 years are probably present in seed form in the field today, so that they should be amenable to recognition and nurturing with a fitting strategy. My line of reasoning will involve a series of wanderings through some of the key advances and paradigm shifts in physical oceanography in the last two decades. Although pragmatism and space restrictions mean that there are many omitted subtleties and unavoidable oversimplifications, the general lessons extracted from the above should hold. The areas of physical oceanography where major advances are to be expected in the light of this argument will be identified as those related to dissipative aspects of the ocean circulation and the role of the circulation in the coupled climate system. The basic elements of a strategy that fosters progress in these areas will be discussed, with an overarching emphasis on the promotion of curiosity-driven fundamental research against opposing external pressures and on the special role of education.
The article is structured as follows. In §2, the fundamental principles of ocean circulation are synthesized minimally in terms meant to be understandable by the non-specialist, as a preamble to contextualizing the evolution of physical oceanography in the last two decades, discussed in §3. Section 4 considers how the lessons drawn from the past may be used in designing a strategy for the future of the field. Finally, §5 summarizes the central message of the paper and comments on the mechanism to bring the strategy to bear.
2. Elementary principles of ocean circulation
The fundamental principles of ocean circulation may be synthesized by stating that the ocean flows because it is forced by winds, tides and exchanges of buoyancy with the overlying atmosphere and cryosphere. Illustrations of this forcing are commonplace in oceanographic textbooks and are exemplified in figure 1. Figure 1a reveals the correspondence between the spatial patterns of the time-mean wind stress and those of the time-mean ocean dynamic topography, indicative of the role of winds in setting the surface ocean circulation. Similarly, Figure 1b shows a well-known, observation-based schematic of the Southern Ocean overturning circulation and its relationship to wind forcing and air–sea buoyancy exchanges that makes apparent the implication of both forcings in shaping the direction of vertical motion of the different water masses.
Physical oceanographers, like other geophysical fluid dynamicists in their respective fields, express the above statement of the causes of ocean flow in terms of a set of equations defining the conservation of fundamental dynamical properties (such as energy, momentum, vorticity and enstrophy (vorticity squared); see  for a recent and lucid review). This equation set derives from the Navier–Stokes equations and, ultimately, from Newton's equations of motion and the first and second laws of thermodynamics. It readily yields the result that, if the ocean is to remain in a stationary state, some form of dissipation or damping of the circulation is required to balance the injection of dynamical properties into the ocean (i.e. the powering of ocean circulation) by the various forcings. Decades of careful study of the dynamical equations of ocean circulation have revealed that the arrest of the circulation occurs on spatial and temporal scales that are much smaller1 than those at which the ocean is primarily forced, which correspond to the large (O(1000–10 000 km)) spatial scales of ocean basins and to the long (seasonal to centennial) temporal-scale characteristics of the atmospheric circulation. The link between these two disparate sets of scales is provided by ocean dynamics, which operate on the intervening range of spatial and temporal scales and, as required for the transfer of dynamical properties between scales, are fundamentally nonlinear.
These elementary building blocks of ocean circulation are summarized in figure 2, and will serve to articulate the subsequent discussion of the evolution of physical oceanography in the recent past, the current state of the field and the design of a strategy for the future.
3. Lessons from the past, for the future
For decades, physical oceanographers have sought to comprehend the fundamentals of how the ocean circulation is powered, how it is damped and how ocean dynamics connects the very different scales of forcing and dissipation. While the last 20 years have seen significant advances on all these three fronts, the thrust of progress has been in understanding the driving mechanisms of ocean circulation and the ocean's ensuing dynamical response, with issues surrounding dissipation receiving comparatively little attention until the most recent past. This defining feature of the evolution of physical oceanography in the last two decades is illustrated in this section with a few selected examples of key problems in which important advances have been made, and the lessons that may be drawn for designing a future strategy are discussed.
(a) Understanding of the ocean circulation as of two decades ago
The state of physical oceanography as of 20 years ago may be summarized by noting that the field was only just starting to evolve from textbook views of the ocean circulation as being quasi-steady, largely laminar and fundamentally unaffected by topography. For example, explanations for the existence of basin-scale gyres across the mid- and high-latitude oceans [5–11] were still firmly rooted in the elegant work of pioneer dynamicists [12,13]. These authors rationalized the occurrence of gyre circulations away from western boundaries in terms of a ‘Sverdrup balance’ between the vorticity imparted on the ocean by the wind stress curl and the change in planetary vorticity of the water flowing meridionally in the gyre interior. In turn, they conceptualized the western boundary currents closing the gyres in terms of a balance between the change in planetary vorticity of the water flowing meridionally in the boundary current and a somewhat obscure frictional process. A schematic of this theorized gyre physics is given in figure 3a.
Around two decades ago, the basic validity of this dynamical description of gyre circulations was seemingly endorsed by the qualitative resemblance between the gyre structures predicted by the theory and those measured in the ocean (figure 3b), as well as by various regional observation-based quantitative tests (e.g. [17–19]; see also discussion in ).
A second significant illustration of the conceptual understanding of ocean circulation characteristic of the early 1990s may be found in the dynamical views of the horizontal flow in the abyssal ocean prevalent at that time. Those views [21–25] were heavily influenced by the model of Stommel & Arons , which rests primarily on the assumption that the structure of the permanent pycnocline is maintained as large-scale upwelling induced by geostrophic flow in the abyssal ocean balanced by vertical diffusion of density, and on the prescription of one distinct high-latitude region of dense water formation in each hemisphere. The Stommel–Arons model's predicted abyssal circulation is shown schematically in figure 4a. Its most remarkable feature is the presence of deep western boundary currents flowing equatorward from dense-water formation sites and of sluggish recirculations directed poleward away from the basins' western boundaries. Regular observations of the existence of deep western boundary currents in various basins (going back to the pioneering measurements of Swallow & Worthington ; see also [31–35]) were commonly taken as evidence that the Stommel–Arons model was an adequate zeroth-order descriptor of the abyssal ocean circulation.
Characterizations of the circulation in the vertical plane as of two decades ago were also founded on the treatment of the oceanic flow as being basically time-invariant, laminar and topographically unreactive. For example, theoretical and conceptual models of the exchanges of water and tracers between the upper ocean mixed layer and the ocean interior [36–41] had strong roots in the ‘ventilated thermocline’ model , which portrays the ventilation of the pycnocline as resulting from the transport along density surfaces (by steady wind-driven Ekman and geostrophic flows) of mixed layer water masses, the properties of which were commonly assumed at the time to be set in a one-dimensional fashion by air–sea buoyancy exchanges and vertical mixing. An illustration of the application of one such model is shown in figure 5a, where the annual-mean subduction rate is calculated for the North Atlantic from wind stress and density climatologies . The diagnosed subduction rate distribution was interpreted to be largely consistent with estimates of the age of upper pycnocline water masses in the region. For example, figure 5b displays a map of a metric of pycnocline ventilation age based on anthropogenic tritium and 3He, which suggests that pycnocline water masses in the North Atlantic are ventilated in the northern part of the domain and gradually age following the anticyclonic (clockwise) circulation of the subtropical gyre , as implied in figure 5a.
Finally, the prevalent paradigm of deep oceanic overturning and the maintenance of the deep ocean stratification in the early 1990s [46–51] reflected the ideas of Munk , who contended that both of those physical features of the deep ocean can be conceptualized as arising from a balance between the sinking of dense waters to the abyss at selected high-latitude regions and the downward transport of buoyancy from shallow and/or intermediate layers by small-scale turbulence occurring elsewhere at a globally averaged rate of O(10−4 m2 s−1) (figure 6a). The apparent inability of the ocean microstructure community to measure sufficiently intense and widespread turbulence in the pycnocline was beginning to prompt the so-called ‘missing mixing’ problem [55,56].
Against this backdrop of an ocean circulation viewed as slowly evolving and largely laminar, the international oceanographic community was initiating possibly the largest and most ambitious oceanographic experiment to date: the World Ocean Circulation Experiment (WOCE; see  for a historical perspective). The conceptual picture of the ocean circulation outlined in this subsection was implicit in the experiment's design and goals. WOCE sought to define, for the first time, the state of the global ocean circulation and its role in the climate system by occupying a global grid of many thousands of hydrographic stations over a decade (figure 7a). The central aim of the experiment was to produce estimates of the time-mean oceanic transports of mass, heat and freshwater by applying inverse estimation techniques to the hydrographic survey (see  for a review of those techniques), ultimately leading to quantitative, laminarized schemes of the circulation such as that displayed in figure 7b. The dynamical paradigm of the ocean underpinning these circulation schemes is still deeply engrained in the collective oceanographic psyche, yet progress over the last two decades has challenged several of its foundations.
(b) Twenty years of progress
Our understanding of the ocean circulation has evolved considerably in the last two decades. A possible summary of this evolution can be attempted by noting that many of the prominent advances in physical oceanography in the last 20 years have stemmed from or implicated the recognition that the dynamics of ocean variability and of ocean–topography interactions are important in shaping the elementary features of the circulation. Most glaringly, the advent of satellite altimetric measurements of the ocean's surface geostrophic flow and of mesoscale eddy-permitting global general circulation models has revealed the ocean to be intrinsically turbulent.2 This is illustrated in figure 8, where it is shown that the surface kinetic energy of the ocean's mesoscale eddy field is an order of magnitude greater than that of the time-mean circulation.
The general finding of the ocean being inherently turbulent and reactive to a range of topographic length scales raises questions on the dynamical meaningfulness of the time-mean ocean circulation, and casts doubt on the value of characterizations of the circulation resting on assumptions of flow laminarity and a lack of leading-order topographic influence. To add some tangibility to this statement, it is useful to consider in brief how the metrics of understanding of the ocean circulation outlined in §3a have evolved in the last two decades. For example, a new explanation for the closure of mid- and high-latitude gyre circulations by western boundary currents has been proposed that does not involve obscure frictional processes at the western boundary, but that instead invokes the inviscid interaction of the flow with topographic slopes on scales of O(100–1000 km) [15,62]. This explanation is endorsed by mesoscale eddy-permitting general circulation models (figure 3c), which reveal that torques exerted by sloping topography on the circulation balance the change in planetary vorticity associated with meridional flow in boundary currents. The vertical transfer of vorticity required to link the net (integrated across a gyre) surface vorticity input by the wind to the net vorticity output at the sea floor has been attributed to the action of mesoscale eddies .
A somewhat analogous illustration of the shift in characterizations of the ocean circulation towards a more turbulent and topographically influenced paradigm is offered by the discovery of fundamental flaws in the elegant Stommel–Arons model (and many of its relatives) of the lateral circulation in the abyss. One key weakness was revealed by the observational finding of turbulent diapycnal mixing (i.e. the vertical diffusion of density balancing upwelling across the deep ocean stratification) being strongly localized by topography rather than spatially uniform [27,64–66] (figure 4b). This and other unrealistic assumptions underpinning the model critically affect its outcomes, such that the circulation patterns indicated in figure 4a are not robust to changes in those assumptions. While the existence in the ocean of the deep western boundary currents predicted by the model is now beyond doubt, their significance as a conduit of dense water masses away from formation regions has been questioned by a variety of observations that highlight the role of mid-basin pathways instead [28,67–69], as illustrated in figure 4c.
The recognition of the central role played by mesoscale eddies (and, most recently, submesoscale flows too) in shaping subduction and ventilation in the upper ocean has arguably afforded the most significant advancement in that subject in the last 20 years [70–76]. Clear illustrations of this point may be found in calculations of time-mean subduction and ventilation in observational and numerical model datasets, in which the inclusion of the effects of turbulent, time-varying flows is critical to reconciling our knowledge of the wind and buoyancy forcing of the upper ocean with tracer-based estimates of the rate of renewal of pycnocline water masses [43,53,77–79]. This point is exemplified by the schematic in figure 5c, which summarizes the results of a study of the mechanisms of North Atlantic pycnocline ventilation based on the measured distribution of the ventilation metric shown in figure 5b. The authors of that study interpreted that distribution as arising from a combination of advection of winter mixed layer waters by the mean circulation and their diffusion by mesoscale eddies, and inferred that the latter process needed to be invoked to explain the measured ventilation of the lower pycnocline.
Stimulated in part by this newly gained understanding of the upper ocean and by widespread observations of weak turbulent mixing in the pycnocline, explanations of deep oceanic overturning and the maintenance of the deep ocean stratification in the last two decades have tended to move away from the essentially diabatic model spawned by Munk's work  towards a largely adiabatic paradigm, in which a wide range of deep-ocean density classes experience significant upwelling along isopycnals in the Southern Ocean [80–86]. Such upwelling is forced by the wind both directly and indirectly, the latter via the action of the mesoscale eddy field generated by baroclinic instabilities of the mean ocean circulation (figure 7b). As these ideas flourished in the oceanographic literature, the missing mixing puzzle was increasingly judged solved or unhelpful, and the problem evolved into a discussion of the rate at and ways in which energy flows through the ocean [87–91].
The shift towards a paradigm of the ocean circulation in which the mean state of the ocean is fundamentally shaped by turbulent aspects of the flow and a range of interactions with topography has been reflected in a change of philosophy in the way the oceanographic community approaches the study of the circulation. The WOCE-era expectation of the existence of a meaningful time-mean ocean circulation addressable with quasi-steady-state inverse estimation techniques with very basic dynamics has been superseded by (i) efforts to estimate the evolving state of the turbulent ocean with complex dynamical models assimilating a wide range of measurements from increasingly more coordinated observing systems [92,93] (see also figure 7c, which illustrates several of the novel technologies—such as the Argo float network , CTD-instrumented sea mammals , satellite altimetry  and gravitometry , and the surface drifter network —that are now routinely used in monitoring the state of the ocean) and (ii) conceptually simpler approaches seeking to understand oceanic adjustment to transitory forcing in idealized situations [99–102]. These two sets of efforts are complementary in that, while (i) focuses on determining the changing state of the ocean as accurately as possible, the picture of oceanic evolution it depicts commonly results from a confused superposition of diverse phenomena, such that deep understanding of how the circulation operates can seldom be achieved in isolation from (ii).
(c) Lessons for the future
An important characteristic of the evolution of physical oceanography in the last two decades, as illustrated by the metrics of understanding outlined in preceding subsections, is its considerable degree of predictability, at least with the benefit of hindsight. Far from being serendipitous, most of the key advances in physical oceanography over that period had seeds that were present either in the field or in a more mature sister field (atmospheric science) prior to the early 1990s.
This point may be demonstrated once again by revisiting the examples above. Thus, the new explanation for the western boundary closure of mid- and high-latitude gyres, which highlights the effect of topographic torques in arresting the ocean circulation and the role of mesoscale eddies in transferring vorticity between the surface and the sea floor, is no more than a generalization of a set of ideas put forward earlier by Munk & Palmén  and Johnson & Bryden , among others (see, for example, the early work on the dynamical balance of western boundary currents by Holland ), in the context of a discussion of Antarctic Circumpolar Current (ACC) dynamics (figure 3d). Similarly, the topographic localization of turbulent mixing leading to some of the failures of the Stommel–Arons model had been suspected prior to its observation in the deep ocean, on the basis of earlier fundamental work on the physical processes underpinning mixing [105–109]. Strong indications of the importance of mid-basin pathways could also be found in the hydrographic literature of the 1980s [29,110] (figure 4d). The incorporation of the effects of mesoscale eddy flows to models of subduction and ventilation in the upper ocean followed naturally from a collection of previous studies of how eddy stirring influences the large-scale potential vorticity distribution of both the ocean and the atmosphere [44,111] (figure 5d). Finally, the notion of substantial adiabatic upwelling of deep waters in the Southern Ocean that was so influential in revisiting the deep ocean mixing problem in the last 20 years had been present in the field for several decades , as evidenced in figure 6c.
In all these cases, and in many others that are not reviewed here, key advances in understanding the ocean circulation occurred not as the outcome of an unexpected or unpredictable breakthrough, but rather as the result of a seemingly obvious (in retrospect) connection of distinct, widely acknowledged ideas. I thus argue that the foremost guiding principles of a strategy seeking to nurture the future of physical oceanography should be to identify the seed concepts of future breakthroughs in today's field, and to foster a research environment that inspires connections between such concepts.
4. Nurturing the future
How may one translate this somewhat academic argument into a well-defined strategy? In this section, I offer specific recommendations on how each of the strategy's two guiding principles may, in my view, be fulfilled. In rationalizing such recommendations, two distinct factors must be carefully considered: (i) the ingenuous, curiosity-driven evolution of scientific ideas, which sets where the boundaries of fundamental knowledge lie at any given time, and (ii) the technological, historical and societal contexts in which scientific investigation is conducted. It will be argued that, while (ii) will inevitably constrain (i) to some extent (and, in doing so, foster important research in some areas), a strategy that is most effective at advancing physical oceanography should bolster curiosity-driven, fundamental research as the factor dictating the field's agenda.
(a) Identifying the seeds of future breakthroughs
The pursuit of any strategy that has fundamental research as its chief priority must commence with the identification of the areas of the field where major boundaries to knowledge lie that appear vulnerable to present intellectual and technological capabilities. One such major area may be identified by revisiting previous considerations on the fundamental principles of ocean circulation (§2) and on the evolution of physical oceanography over the last several decades (§3). In that discussion, it is evident that a common thread to progress in understanding the ocean circulation in and prior to the last 20 years is the passive, end-of-the-road role attributed to the dissipative and damping processes arresting the circulation (with the exception of the connection between small-scale turbulent mixing and large-scale oceanic overturning, the importance of which has been downplayed over time). For the vast majority of the foremost problems in physical oceanography, the rate-controlling role lies elsewhere.
There are, in my view, two reasons for the historical disregard of dissipative/damping processes as an active factor in ocean circulation. First, the study of such processes, which in most cases are associated with the smallest length scales and shortest time scales of the circulation, is greatly complicated by logistical and technological difficulties in observing and modelling flows on those scales. Second, and perhaps as a result of such difficulties, the development of physical oceanography appears to be underlain by the tacit, untested assumption that the evolution of the ocean's state over time scales of concern to humankind (up to centennial?) is largely independent of dissipative/damping processes. While recent technological advances in ocean observation and computing mean that it is becoming feasible to address an increasing number of problems involving dissipative and damping processes, the assumption of those processes' passivity in ocean circulation is being challenged by a mounting body of circumstantial evidence.
The most fundamental of this evidence may be found in the chaotic systems field, which studies the dynamics of idealized forced–dissipative nonlinear systems (the ocean being one such system). There is a substantial literature in that field ([112–117] provide some examples of direct geophysical relevance) that demonstrates that the mean state and evolution of forced–dissipative nonlinear systems are sensitive to dissipative processes over a wide range of conditions, where the sensitivity arises from a variety of upscale control mechanisms involving the modification of mid-scale nonlinear terms by parametrized small-scale processes. An illustration of this general result may be found in figure 9, which is taken from . There, it is seen that two simulations of turbulent forced–dissipative flow in a rotating sphere with different forcing and dissipation may display the same mean state (as measured by the total energy and number of jets) yet very different flow dynamics (as apparent in the jet behaviour). This example illustrates in simple terms how any two ocean general circulation models tuned to the same ‘realistic’ mean state may readily display different physics and sensitivities as a result of having distinct representations of dissipative processes.
Other examples of the relevance of dissipative/damping processes in shaping the basic features of the large-scale circulation may be found in the atmospheric literature. For instance, studies of the basic dynamics of the Southern annular mode (SAM; the dominant mode of extratropical atmospheric variability in the Southern Hemisphere, involving vacillations of the westerlies across the troposphere and stratosphere on a wide range of time scales, e.g.  and references therein) reveal that the reason many atmospheric general circulation models fail to represent the properties of the SAM correctly despite resolving the range of energy-containing scales of the circulation is the sensitivity of the eddy–mean flow interactions that shape SAM characteristics to details of how eddies are dissipated in the models [119,120].
Suggestions that these general lessons drawn from the chaotic systems and atmospheric literatures are likely to apply to the ocean are offered by a variety of recent illustrations of how dissipative processes influence the way in which mesoscale eddy variability moulds the mean circulation. For example, there is mounting evidence of unbalanced motions and small-scale turbulent processes playing a significant role in defining the characteristics of the mesoscale eddies and Rossby waves that mediate oceanic adjustment to forcing and internal resonances [121–129] (figure 10). Similarly, a growing body of work points to the existence of a zoo of three-dimensional submesoscale phenomena that are key in defining the upper ocean's response to forcing in the presence of the mesoscale structure characteristic of much of the ocean [76,131–136], as exemplified in figure 11.
It is on the basis of this emerging recognition of dissipative/damping processes as playing a controlling role in ocean circulation that I postulate that the research of these processes is poised to be the focus of most major advances in our understanding of the circulation in the next two decades. That is, in my view, where the ingenuous evolution of scientific ideas would take the field in the absence of steering by contextual factors. An appeal for the protection and promotion of this area in a future strategy will logically follow. Such an appeal, however, would border on the naive if placed without consideration of the technological, historical and societal contexts in which physical oceanography is presently immersed. These may be summarized by noting that the field is now at a juncture in which technological advances in ocean observation and modelling (in particular, the advent of coordinated observing systems and complex data assimilative models), the field's own coming of age into a mature branch of geophysical fluid dynamics, and the growing societal concern for the future evolution of the Earth's climate and environment conspire to drive physical oceanography towards a more operational and multi-disciplinary enterprise. While this will undoubtedly lead to major opportunities to advance our understanding of the role of ocean circulation in decadal climate variability, it will also endanger progress on fundamental areas that may not be of immediate consequence to ocean state estimation or decadal climate prediction (such as the problems related to dissipative/damping processes outlined above) by diverting resources away from those areas. A major challenge for any future strategy will be to recognize the vulnerable position of fundamental research against such background pressures, and to administer this tension in a manner that attaches value to basic understanding of how the ocean works, regardless of its short-term impact on applied problems.
(b) Implications for the design of a strategy
We may draw the preceding discussion to a conclusion by identifying its implications for the design of a strategy for the future of physical oceanography. I have argued that, if such a strategy is to inject creativity and dynamicism into the field, it must hold the promotion of fundamental research as its prime directive. While the definition of ‘fundamental research’ should by nature not be overly restrictive, the distinctive standing of the ocean circulation's dissipative/damping processes as an area where major progress is highly plausible in the medium-term future should be acknowledged. In order to promote a research environment that inspires the occurrence of breakthroughs, curiosity-driven enterprise and risk (often precursors of genuine innovation) should be encouraged to a reasonable degree, rather than penalized. In this context, the essential scientific tenet that any breakthrough must ultimately be underpinned by a new hypothesis verified with novel observations should be recognized and cultivated, as should the key role of technological advances in providing such observations. Topical illustrations of risky, innovative and high-yield science supported by technological creativity abound in the study of dissipative/damping processes. For example, seismic imaging of the water column, microstructure measurements from autonomous vehicles and wide-swath altimetry now appear to be on the verge of transforming our understanding of several of those processes.
As reasoned above, a strategy that seeks to nurture the future of physical oceanography must not only define the broad areas of and means to achieve major advances in the field, but also identify external pressures and, to the extent that these may be inevitable, embrace them and extract opportunities from them to advance fundamental understanding. Among these external pressures, the growing culture of accountability, success metrics and demonstrability of impact in the administration of science across many nations looms as a major threat to the advancement of fundamental research. It is troubling to see early career scientists promptly learning that in order to succeed in science one has to ‘play the system’, the emphasis shifting from depth of knowledge and original thinking to scoring highly against various one-dimensional metrics.3 This culture appears to be founded on the assumptions that innovation and creativity can be commissioned and measured precisely, and that doing so optimizes the societal benefits of scientific enterprise—ignoring the fact that the distinction between fundamental and applied science is almost without exception a mere matter of time scale. In the arts and humanities, these assumptions are widely considered inappropriate (e.g. , for an overview of the present debate on the measurability of art), yet they are increasingly engrained in the management of scientific disciplines that arguably thrive on the same human qualities (e.g.  for an in-depth discussion of how centralized metrics suppress creativity in science). An effective strategy for the future of physical oceanography must be tasked with combating these damaging practices by defining a specific set of values—aligned with the considerations at the start of this subsection—by which the merit of research in the field may be assessed.
A further implication of the discussion in §4a is that the present-day steering of physical oceanography towards a more operational endeavour by external factors should be acknowledged by the strategy. The strategy should advocate that the growth of this area does not occur at the expense of research of the fundamentals of how ocean circulation works, and that research of this nature be incorporated into the ocean state estimation enterprise as much as possible, via more simplistic, idealized studies that may facilitate interpretation of the inferred oceanic change in terms of elementary dynamical processes (e.g. see discussion in §3b). It should be stated that the advancement of our understanding of the role of ocean circulation in climate variability will only be maximized if such a dual approach is adopted. In this regard, the physical oceanography community would do well in drawing a cautionary tale from the development of atmospheric science in the last three decades. It is obvious to the external onlooker, as well as to many senior scientists in the field, that progress in fundamental understanding of the atmospheric circulation has decelerated drastically in that period, as financial, technical and (most critically) intellectual resources have increasingly been diverted towards the engineering and evaluation of complex data assimilative models with comparably poor yield in fundamental understanding. This occurrence ultimately stems from a basic disassociation between increasing complexity and understanding in science: in order for an enhancement of the resolution or sophistication of numerical simulations (or, for that matter, of observations) to advance understanding, the complexity that they capture needs to be broken down into pieces that are genuinely comprehensible by the human brain.
Finally, and perhaps most importantly, a strategy for the future of physical oceanography must establish the importance of educating the coming generations of physical marine scientists in fundamental research, regardless of whether their subsequent career path is aligned with the pursuit of research of that nature or otherwise. This is to guarantee that all early career scientists gain a basic appreciation of the details of how ocean observations are made or how the code of numerical ocean models is formulated, as well as of how those methodological issues shape our attempts to understand the ocean. It is argued here that the implication of fundamental research in the growing area of ocean state estimation and the guarding of physical oceanography against the external pressures described in the preceding paragraphs are contingent on a successful education of the future generations of physical oceanographers in an environment where the attainment of fundamental understanding is the ultimate aspiration.
In this article, I have sought guidance in the past evolution of physical oceanography to define the basic elements that a strategy for the future must contain to nurture the advancement of our fundamental understanding of the ocean circulation through creativity and innovation. On the basis of that guidance, I have argued that there are parallels between the transition towards a view of the ocean as turbulent and topographically reactive of two decades ago and today's emerging recognition of dissipative and damping processes as playing a controlling role in the circulation. I have reasoned that since major advances in physical oceanography appear to occur primarily as the result of somewhat obvious (with hindsight) connections between distinct, widely acknowledged ideas, the seed concepts of future breakthroughs should be present in today's field. Thus, to promote the occurrence of breakthroughs, the strategy's mission is to identify their seed concepts and to foster a research environment that inspires connections between these.
I have postulated that the areas that are poised to be the focus of major breakthroughs in physical oceanography over the coming two decades are those related to dissipative/damping processes and the role of the ocean circulation in the coupled climate system. While the former signals the most evident boundary of curiosity-driven scientific knowledge that appears susceptible to current intellectual and technological capabilities, the latter follows from the present drive of physical oceanography towards a more operational enterprise by contextual factors. The strategy must be tasked with achieving a balance between the development of the two areas by holding the promotion of fundamental research as its prime directive against external pressures; encouraging ingenuous and risky science to a reasonable degree; defining a general approach to extract process-related knowledge from ocean monitoring and state estimation activities; and establishing fundamental research as the apex of education for the future generations of physical marine scientists. A final important remit of the strategy must be to contest the growing culture of accountability in the administration of science by putting forward an alternative set of values—aligned with the theses above—by which the merit of research may be assessed.
To conclude, it is important to emphasize that a strategy is only effective in steering a scientific field if it is implemented by the management (particularly the administration of funding) of that field. I commend this joint project between the Challenger Society for Marine Science and the UK Scientific Committee on Oceanic Research to not stop at consolidating a documented strategy for the future of oceanography, but to firmly press the case for its adoption by the field's management leadership.
I wish to thank the Challenger Society for Marine Science and the UK Scientific Committee on Oceanic Research for offering me the opportunity to take part in their ‘Prospectus for UK marine science for the next 20 years’ joint project. I am grateful, in particular, to the organizing committee of the initial project meeting (Harry Bryden, Gwyn Griffiths, Carol Robinson and Terry Sloane), and to David Marshall and Ric Williams for their supportive reviews. The views presented in this article have been coloured by informal conversations and discussions with many friends and colleagues over the years. For these, I am very thankful, though I caution that none of those individuals should be held responsible for any opinions expressed here, or any flaws in my arguments.
One contribution of 11 to a Theme Issue ‘Prospectus for UK marine science’.
↵1 Note that the spatial and temporal scales at (and the mechanisms by) which the arrest of ocean circulation takes place are dynamical variable-dependent (for example, energy is dissipated by three-dimensional turbulent overturns with broadly characteristic spatial and temporal scales of O(1 cm) and O(1 s); in turn, momentum is removed from the circulation primarily as mesoscale flows with temporal scales of O(100 d) flow around topographic features O(100–1000 km) across).
↵2 Strictly speaking, the realization that the ocean contains an energetic mesoscale dates back to a series of in situ experiments in the 1970s and 1980s, initiated with the Mid-Ocean Dynamics Experiment (MODE; see  for an overview). However, the lack of synoptic data on the oceanic mesoscale (from observations or models) prior to the 1990s meant that the ocean had to be treated as quasi-steady for most practical purposes, thus resulting in a very limited appreciation of the mesoscale's role in the dynamics of the ocean circulation.
↵3 A well-known example of how current metrics often fail to capture the true value of scientific research is provided by one of Henry Stommel's most influential papers, which discusses the existence of multiple stable states in simple models of the thermohaline circulation . This work was cited only three times in its first 25 years after publication and hence, by any modern objective measure, would be considered a poor paper (see  for a discussion).
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