Perspectives on the November 4-5 Workshop
from the Florida Bay Oversight Panel
Ad Hoc Committee on Higher Trophic Levels

Linda A. Deegan, Chair
The Ecosystems Center
Marine Biological Laboratory
Woods Hole, MA 02543

Scott Holt
University of Texas at Austin
Marine Science Institute
750 Channel View Drive
Port Aransas, TX 78375

Joshua Sladek Nowlis
National Marine Fisheries Service
Woods Hole, MA 02543

Susan M. Sogard
National Marine Fisheries Service
Hatfield Marine Science Center
2030 Marine Science Drive
Newport, Oregon 97365

Submitted to the Program Management Committee
Florida Bay Research Program
8 January 1998

Concerns about the status of higher trophic levels in Florida Bay stem from declines in population levels of some living resources, especially fishes, indicating that the Bay's capacity to support them is declining, or from observed degradation of habitats deemed important to these resources. Because of these concerns and the importance of commercial and recreational fisheries in the economy of the region, studies on the relationship between environmental change and the support of higher trophic levels is a major element of the Florida Bay Research Program. The objective of the Research Program is to guide the restoration of Florida Bay. It is directed by a Program Management Committee (PMC) representing state and federal agencies sponsoring research and monitoring in the Bay.

On November 4 and 5, 1997, the PMC convened the Florida Bay Higher Tropic Levels Workshop in Miami, Florida, to review progress on the component of the Florida Bay Program based primarily on Central Question #5: "What is the relationship between environmental and habitat change and the recruitment, growth and survivorship of animals in Florida Bay?" (Florida Bay Program Management Committee 1997). This question addresses the particular concern that ecosystem shifts within the Bay have affected the productivity of animals with important ecological, commercial, or recreational value. Participants included investigators and program managers working on higher trophic levels in Florida Bay, and an ad hoc committee consisting of four members. The four individuals on the ad hoc committee included one member of the Florida Bay Research Oversight Panel (Dr. Deegan) and 3 others invited because of their experience in population biology or modeling. The stated goal of the workshop in the letter sent to ad hoc committee members was to develop a comprehensive conceptual model; however, the design of workshop placed ad hoc committee members in the position of evaluating a work plan.

A total of 15 presentations were given at the workshop. In addition, other workshop attendees contributed information and perspectives from the floor during discussions. The presentations were quite uneven in their accomplishment of the goals of the workshop. The committee did not review each study or presentation, but focused on the overall program plan. The reviews of the Florida Bay ecosystem's problems and studies addressing non-upper trophic levels components were sufficiently thorough and informative. The presentations on higher trophic levels components were mixed; some were reviews of past studies in Florida Bay, some were proposed studies/models to be done in Florida Bay, and some were reviews of studies (or models) conducted elsewhere that might have applicability to Florida Bay. The Panel found that it was often not clear which was which. Given that, a comprehensive evaluation of the approach the Florida Bay science program is taking in the study of higher trophic level dynamics will, itself, be uneven.

The ad hoc committee saw a high level of interest by federal and state agencies, scientists and the public for this component of the research in Florida Bay. The committee also recognizes that there are several excellent individual research projects being carried out in Florida Bay and good cooperation and information exchange between researchers. Notable attributes of the plan for work on higher trophic levels include:

• Integration of independent studies into a more Bay-wide view of higher trophic levels.
• Recognition that Florida Bay can be partitioned into regional zones that have their own functional dynamics.
• Cooperation and data sharing among researchers.

In the same constructive spirit that lead to the convening of the workshop, the ad hoc committee also recognizes that improvements in the research plan are possible. Areas that need more effort include:

• Development of a comprehensive conceptual model of the interaction between ecosystem dynamics and higher trophic levels.
• Hypothesis driven research
• Definition of program restoration goals.
• Stability of long-term data collection .
• Prioritization of program elements and their funding.

The sections of the report that follow provide the ad hoc committee's assessment and offer guidelines for improvement of these areas.

Development of an integrated comprehensive conceptual model of the interactions between ecosystem dynamics and higher trophic levels in Florida Bay should be the first priority of the Higher Trophic Level Research Team. The Florida Bay Oversight Panel report of February 17, 1997 suggested that it is essential that a conceptual model of higher trophic level components in Florida Bay be developed. They recommended a workshop be convened to: 1) synthesize existing information, 2) identify key processes, and then 3) develop a strategic plan for integrating these processes into a numerical model. The March 1997 Strategic Plan included as a program element: "a workshop will be conducted in mid 1997 to: (1) develop conceptual models of consumer processes relative to habitat, environmental conditions and water management, (2) select representative species for modeling, and (3) determine model needs and model focus." The October 22, 1997 letter to higher trophic levels panel members restated the above Strategic Plan element as the purpose of the November 4-5 workshop. However, the organization and conduct of the November workshop was not designed to accomplish those goals. The one and a half days of presentations seemed to have as their goals to: 1) provide the review panel with an historical perspective of the Florida Bay's problems, 2) provide an overview of studies and approaches to non-upper trophic levels ecosystem components, and 3) provide a comprehensive summary of what is planned in the immediate future for higher trophic levels studies, with the intent that the panel would offer an evaluation of the approach.

There was some confusion over the role of the November workshop. The November workshop was clearly a panel review of the existing or proposed program and not a workshop to develop ideas. Because of time constraints, workshop format and directions from the workshop chair, little open scientific dialog occurred. On several occasions only questions from the ad hoc committee were allowed. A meeting was apparently held prior to the November workshop, but its goal was apparently planning the presentations for the November workshop rather than addressing the more general question of, "What controls higher trophic level production in Florida Bay?" The planning meeting did not appear to have had the participation of the one or two ecosystem "thinkers" and one or two modelers from outside the program as suggested by the Oversight Panel, nor did it appear to have included many of the higher trophic levels investigators. Such a comprehensive workshop would have been very useful before we came in, but would still be beneficial now.

The research team approach is an essential element of the development of an integrated program. While encouraging progress has been made, it is clear that the higher trophic level team building process is just beginning. We urge that continuation of this process be given highest priority and that more researchers be involved in the team. Here again there is a substantial need for experimental data applicable to specific components of the models. The controlling variables and their mechanism of control need to be considered more explicitly.

The Panel believes that gathering the varied projects directed at higher trophic level organisms under the general umbrella of a broad modeling effort is a positive step. Data collection has been fairly extensive in the Florida Bay ecosystem and a modeling effort can help pull it all together into a coherent package. One of the principal outcomes of modeling is often a more tightly focused set of questions. We see this as one of the primary benefits of this modeling effort. However, while the Panel applauds the development of higher trophic level models as a means to direct research to answer key questions, we must also raise caution concerning false expectations and over-reliance on models. Models are approximations and do not always give good predictions of the outcome of management schemes. They work best when their predictions and underlying assumptions are linked to ongoing field investigations. It is appropriate at this stage to define realistic expectations from the higher trophic level models. It is also important to maintain high quality data collection not only to calibrate and check model predictions, but as an independent assessment of the restoration plan.

There did not appear to be a major effort to incorporate a wide variety of ecosystem dynamics in the higher trophic level modeling effort. Interestingly, the current emphasis on salinity seems to be a response to a previous review by the Florida Bay Science Review Panel (Boesch et al. 1995, 1997). The previous reports commented that the higher trophic level work seemed to exclusively focus on seagrass die off and ignored other important environmental variables. Those reports gave extremes in salinity as an example of other important variables. In these presentations we see an overly narrow focus on salinity, with little explicit consideration of other factors. For example, why is O₂ not included as a forcing function in the single-species models? O₂ concentration may be largely controlled by temperature and salinity levels but the spatially variable occurrence of plankton blooms may substantially alter that relationship. O₂ data may be more difficult to obtain over a broad scale than temperature or salinity, but may be critical.

The major tenet that understanding the effects of salinity levels on ecosystem function will be the key (or even sole) goal of the program is too narrowly focused. While salinity itself can have direct impacts on physiological function, the estuary is populated largely with euryhaline organisms that are quite tolerant of salinity variations. Only extremes in salinity would be expected to produce extensive ecosystem impacts and these extremes are occurring and need to be understood. However, much of the variation in ecosystem dynamics will remain unexplained if salinity is the considered to be the major forcing function. Salinity may serve as a surrogate for other factors such as water flow, particle transport, nutrient distributions, etc. but it is not a perfect substitute. The high evaporation/precipitation ratio at some times of the year make using salinity as a surrogate for other types of water movement quite problematic. Even with the emphasis on salinity, there seemed to be lack of empirical studies relating salinity to changes in community structure or population dynamics relative to the strong emphasis of salinity as the driving force in modeling efforts.

The higher trophic levels considered in developing the conceptual model need to be broad. The only higher trophic levels that seem to be considered are fish or fishery species such as pink shrimp. There is no information on intermediate trophic levels such as amphipods, isopods, snails and other small invertebrates. These consumers can be important as mesoherbivores that can control microalgae (both benthic and epiphytic) and are important prey items for higher trophic levels. This is a major data gap that needs to be filled. There appears to be a lack of interest in bird populations, yet they are the most visible component of the Florida Bay ecosystem for the general public. A more explicit plan to extend the wading bird portion of the ATLSS program into Florida Bay is warranted. Coordination with the extensive databases on prey fish availability should be made. Shifts in the physical location of forage fish from the surface to the bottom or vice versa can have important consequences for wading birds which are limited in the depth of water in which they can effectively feed. Wading birds also provide a link between the Everglades and Florida Bay. Shifts in their foraging behavior, contrasts in nesting success in different locations, and overall population fluctuations can be more readily documented than for aquatic residents and may be highly informative regarding the influence of different management practices.

The focus on a few key economically-valuable species is understandable; however, understanding the role of other species such as benthic invertebrates and plants in nutrient cycling and algal bloom dynamics is also critical. The choice of what specific species to include in the models were generally not addressed, except for the single species models for pink shrimp and spiny lobster. The choice of what species to include in modeling will clearly be driven by the amount of information available, but no discussion was presented to justify the current selection of species.

Throughout the higher trophic level program, there appears to be little effort expended at understanding larval stages, both in terms of availability (transport processes) and in terms of growth and survival (water quality processes). Incorporation of the available larval distribution data into modeling efforts is vital, as well as information from the circulation model that relates to larval transport. Physical limitations to recruitment by postlarval stages should not be confused with poor habitat quality. Growth data and metabolic rates, as proposed by the Beaufort Lab for spotted sea trout, would be very useful and should receive sufficient effort, perhaps expanded to other species. This information should be an integral part of the modeling efforts. Some experimental work examining water quality effects on larval growth and survival would also be very useful.

Ecosystem effects of trophic interactions resulting from the switch from seagrass/benthic algal-based primary producers to phytoplankton production are not addressed. The proposed package of models includes a "trophic structure/flow analysis" but the presentations at the meeting did not make it clear how (or by whom) those were to be done or what priority it will have. Fundamental changes in trophic structure could be a major component of the ecosystem changes in Florida Bay. There is, however, a striking dearth of information on primary and even secondary consumers in Florida Bay on which to base a trophic structure model. One approach might be to ask the very specific question: Has the shift in forage fish energy flow from benthic to pelagic pathways affected the production of spotted sea trout?

No consideration is being given to any form of top-down control by higher trophic levels despite suggestions that spatial and temporal fluctuations in the benthic grazer community could be an important control on phytoplankton bloom conditions [Florida Bay Oversight Panel 1996 Report]. The approaches proposed are still primarily observational and focused on documenting the pattern of higher trophic level production. In the next phase, these investigators should move towards defining the underlying mechanisms that control higher trophic level productivity and look at controls on ecosystem processes by higher trophic levels.

The modeling initiative proposes a four-pronged approach, including dynamic single-species models, dynamic predator-prey models, community models, and dynamic multi-species ecosystem models. Multiple approaches can be valuable for complex problems, and the problem of human impacts on Florida Bay is no exception. There are many potential impacts and each can operate on different levels. Moreover, insight can be gained about a particular impact by examining it on multiple levels. Each of these approaches is expected to provide insight ultimately into how management of human activities may influence the productivity and ecosystem functioning of Florida Bay.

The Panel feels that multiple-type and multiple-level modeling approach is sound. However, it was unclear which research efforts will actually be conducted or continued. If our understanding of what was presented is correct, only the Pink shrimp single-species modeling and Ulanowicz trophic flow model have any assurance of continuation.

A disconcerting part of the modeling section was an emphasis on the modeling technique over the question that needed to be answered. What this program really needs are some clearly stated questions about how observed or expected physical or biological changes may affect the animals of Florida Bay. For each question of interest, a modeling approach should be tailor-designed to address this particular question. The key processes identified by the models as well as their predictions should then be tested in the field. As an example, the existing single species pink shrimp model does a terrific job of demonstrating that fluctuations in salinity and to a lesser extent sea temperature within Florida Bay can affect its productivity as a nursery ground. This study now needs better laboratory measurements of growth and survival across a greater range of salinities and temperatures. It also needs field tests to see whether the differences in productivity in the field can be adequately explained by changes in salinity and temperature alone.

The modeling efforts apparently do not take full advantage of some useful existing data and models on the physical attributes of the system, or of identified quantifiable habitat attributes. If the link between water management and productivity is the key question for this initiative, then there are several sets of relationships that should be integrated. First, what is the link between the physical system and management activities (here this would primarily involve freshwater management but it would also be interesting to explore the effect of the Keys causeway)? This is being covered by the existing physical models. Second, what are the links between the biological and physical systems? This is the charge to the higher trophic level team. This second question can include direct effects (i.e., population models) and indirect effects (i.e., community or ecosystem models). Third, something that has not been addressed in any of these models, how does fishing pressure (amount and distribution) affect productivity? Finally, note that productivity can be influenced by reproductive output, not just survival and growth. In fact, for most systems, reproductive output plays an important role in productivity, yet this issue (e.g., larval supply) has not been raised.

The general hypothesis underlying the models, as stated in the planning proposal, at present is very broad and perhaps encompasses too much to allow focused testing. A more productive approach might be to erect specific hypotheses that can be directly tested and accepted or rejected. For example, ruling out a factor such as direct effects of salinity on growth may be as useful as attempting to include all possible effects on growth. However, the focus should not be so narrow that synergistic effects are missed. For example, synergistic effects of temperature and salinity on a variety of bioenergetic measures seem likely. Likewise, habitat effects on survival and growth may not operate in concert (ecological trade-offs). For example, growth in seagrass habitats may be poor, but survival high. Salinity may affect pink shrimp survival, and single-species models could predict how salinity might influence productivity based on this mechanism. Alternately, salinity may affect habitat distributions which indirectly affect pink shrimp growth and survival, and community or ecosystem models would be required to study how salinity might influence productivity via this mechanism.

Most of the proposed and developed models are not dynamic, but static. In order for a model to be dynamic, there have to be feedback loops in the model structure. As is evidenced by the model diagrams presented in the Planning Proposal (Browder et al., 1997, Figs. 1 and 2), these models contain no loops. Static models are useful for describing the current state of a system. However, they are not capable of predicting future changes. It is not necessarily bad to focus on static models as they often help in the development of dynamic models. But a plan to get from static models to dynamic models was not presented.

It is not clear how some of the models will be validated and how their predictive capability will be tested. Some means of determining whether or not a model can be effectively be used by management interests needs to be established. The simulation of secondary production via these models would be more reliable with better support from experimental studies.

Single Species, Pink Shrimp: The current model is static, linking temporal and spatial variation in temperature and salinity with growth and survival and thus productivity. This model is perhaps most useful because it shows that these conditions alone can have a large effect on pink shrimp productivity. This study would benefit from better laboratory/field measurements linking temperature and salinity with growth and survival, and from field validations to see if spatial variation in productivity matches model predictions. Future directions for this model will include everything but the kitchen sink; however, incorporation of other factors was not evident in the work plan. Future directions could use some prioritization and would benefit from integration with the comprehensive conceptual model to be developed.

Single Species, Spiny Lobster: The current model is static, involving detailed spatial information gathered over many years. The lobster model in particular appears to be well supported and has made significant progress in predictive capabilities. It offers the researchers a mechanism for summarizing and integrating their findings. Its success is attributable to solid, hypothesis-driven components that have been thoroughly tested via field experiments. It displays an admirable blend of empirical data with predictive modeling. The research team developed specific hypotheses about potential controlling variables and used well-designed experiments to test them. The results were then directly applicable to incorporation in the model. The model thus has a comprehensive background and relevant predictive power. They propose to expand the model to include the effects of seagrass mortality. This expansion will allow integration of additional field studies. They also propose to link their model to circulation models of the Bay, and this link could offer the potential for some more significant analysis. Here, the researchers should focus on producing realistic simplifications of their initial model for incorporation into the circulation model. This will be done more effectively if the models are truly joined, not simply linked but separate as proposed.

Predator-Prey: The current model has been developed for Biscayne Bay and is apparently dynamic. Future efforts could adapt the model to Florida Bay. However, it too involves a fair degree of complexity. As with the proposed single-species models, this one needs conceptual focus. The goal shouldn't simply be to produce a realistic-looking population, but to better understand how, through predator-prey interactions, physical changes in Florida Bay may affect productivity of important species.

Community: The community approach testing spatial aspects of species composition was described in the planning proposal but not discussed in detail at the workshop. The methods will focus on absolute effects of salinity, stratified by habitat. It would be useful to reconsider this approach in connection with prior attempts to derive abundance relationships with various physical and biological variables. The current model is static and proposes to include nearly exhaustive information. Consequently, it is limited in its analytical capabilities. Moreover, the numerous links between species will have important effects on the model's predictions, and few if any of these links are well understood. Proposed changes to the model involve the addition of more information. The potential roles of physical transport and consequent larval availability are especially pertinent in this type of analysis. Likewise, the recent history of salinity at a particular site may be more relevant than the salinity at the time of collection. Incorporation of the hydrodynamic/circulation model for Florida Bay would be valuable here. This approach can be useful as a tool for identifying gaps in our empirical knowledge of community links. However, gaps could be identified as easily with conceptual models that don't involve coding or analysis. Community-level modeling could potentially add useful analytical insight. As with other levels, this will only happen when models are tailor-made and simplified to address particular questions.

The complexity of the subtropical to warm temperate fauna of Florida Bay may overwhelm attempts to fill in the multitudinous compartments of the trophic network model. The application of this modeling effort to management concerns and predictive capability under varying hydrologic manipulations needs careful consideration. Any means of simplifying this approach with a focus on more general categories rather than individual species may be useful. Are there strong interactions between key species that can override the many weak interactions?

Dynamic Multi-Species: This level of modeling is proposed but not done. It would be premature at this time to spend much effort on this model, although specification of its goals could guide the development of species and community models that will form the framework for it. This could produce some great insights. Field data show that sites can be grouped by physical characteristics or by benthic communities, each producing distinct zones within the Bay that apparently overlap nicely across techniques. This evidence suggests that physical processes may indeed be important in establishing ecosystem differences in the Bay. With focused questions, detailed examination of existing and ongoing field studies, and question-specific models, this level of model could produce the most interesting insights within the entire program. It will require multidisciplinary efforts to quantify habitat characteristics and animal communities, and joint field-modeling studies to link these to physical characteristics.

Clear goals and objectives need to be set for the higher trophic level studies. Clear restoration goals with regard to seagrass habitat and water quality need to be established for the resident fishes and invertebrates. Community modeling might proceed with the objective of determining such factors as what levels of turbidity are acceptable for the preferred communities of Florida Bay, what characteristics of seagrass can be used to monitor its recovery as a nursery habitat, can detritus loads reach unacceptable levels for the seagrass residents, what salinity fluctuations are acceptable without perturbing the community, etc.

The planning proposal for higher trophic levels ecosystem modeling does not seem to be driven by restoration goals for the ecosystem (or for higher trophic level organisms specifically). Such goal setting is essential to drive the questions being addressed, to guide decision making in terms of restoration activities, and to evaluate whether restoration activities have had expected results. It appears that many investigators' goals or targets are to return Florida Bay to prior or pristine status. However, the environmental conditions of the pristine status are not known, presenting a moving or even undefinable target. The modeling efforts should be driven by a set of questions like those given on the last page of the higher trophic levels planning proposal for the trophic interactions but stated to address generalized ecosystem function. Critical Question # 5 is too broad to drive specific research questions.

Long-term data collection needs to be guaranteed. The higher trophic level team needs to develop a set of key driving variables and must have higher trophic level data requirements. Much of the higher trophic level data is being collected to meet other research needs. Some programs have been in place for a while, others are occasional, and others are one-time snapshots. A portion of the budget needs to be allocated to insure that critical data are taken consistently over the long term, even if it cuts into the important effort now underway to address processes and mechanisms through modeling. The Panel encourages tight linkages between on-going modeling efforts and data collection, but cautions against collection of data solely to fit the proposed models.

Data collection/analysis should be addressed on a system wide basis. A comprehensive GIS system should be implemented to provide spatial coherence to the data. Many questions about changes in habitats, populations and communities could be addressed within the context of a GIS system. A modeling approach clearly requires an extensive data set for calibration and then verification of the models. The activities presented in the Planning Proposal did not include a process for coordination of data accumulation, quality assessment, or direction for new data collection. A project coordinator (or team) is needed to oversee that process to provide efficiency in collecting both extant data and developing new data. It is not clear whether prior work has been based on a "defined need" basis or on projects (however well conceived or executed) that were simply of interest to the investigators. A coordinated approach should be applied to issue something like RFP's for specific projects designed to deliver data identified as critical through the conceptual model/ecosystem model approach. Sensitivity analysis applied to preliminary models can show where the greatest information gain can be acquired for the effort (and money) invested.

It would be very useful to make a concerted effort to coordinate disparate GIS databases into a single application. If accessible to all researchers, such a database would be of tremendous utility in examining potential spatially correlated relationships of various physical and biological variables. The heterogeneous nature of Florida Bay makes it particularly appropriate for such an analysis, and rigorous use of latitude and longitude coordinates to describe site locations would eliminate confusion over which subenvironments are being examined. If possible, inclusion of physical attributes included in the circulation model (i.e. basin residence times, tidal amplitude, sea level) would be especially valuable in examining the role of larval transport as a controlling variable.